Buccal Misoprostol During Cesarean Section for Preventing Postpartum Hemorrhage: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Buccal Misoprostol During Cesarean Section for Preventing Postpartum Hemorrhage (NCT01733329), a randomized phase 4 study. The primary outcome is Need for Additional Uterotonic Medications.

2. Clinical Question

The question is about a clinically triggered intervention, not simply a laboratory measurement or a direct measure of blood loss. A request for additional medication could reflect findings such as atony or blood loss, but the registry definition also explicitly counts additional oxytocin. The outcome therefore represents the use of further uterotonic treatment under the trial’s stated definition.

The registry lists uterine atony, postpartum hemorrhage and blood loss among the secondary outcomes. Those outcomes offer related but distinct ways to describe events during the same clinical setting. Their presence does not make them interchangeable with the primary endpoint: the primary endpoint is specifically the need for additional medication, while the secondary endpoints describe clinical conditions or blood loss.

3. Trial Design

The registry identifies this as a Phase 4, randomized, double-blind, parallel-group trial. The listed status is completed. The recorded enrollment is 123. The arm descriptions each list n=60, and the registry record does not explain the difference between the enrollment field and those arm entries.

Participants were women with risk factors for uterine atony undergoing cesarean delivery. The misoprostol arm received 400 mcg as 2 buccal tablets, and the folic-acid arm received 10 mg as 2 buccal tablets. The tablets were placed after umbilical cord clamping by the anesthesiologist. The brief summary calls the design placebo-controlled, but the actual comparator arm is named Folic Acid; the registry record does not reconcile that wording.

The listed start is 2008-02 and primary completion is 2013-12. The study’s objective, as recorded, was to assess whether buccal misoprostol during cesarean delivery affected the need for additional uterotonic medication, uterine atony and postpartum hemorrhage. Blood loss is also listed as a secondary outcome. The primary outcome timeframe is 24 hours.

Randomization and double masking are stated design features, but the registry record does not report the allocation procedure, how masking was maintained, or who was masked. The record also does not describe the original sample-size justification, the planned statistical analysis in sufficient detail, or any interim analyses. These omissions limit assessment of how the completed trial followed its intended protocol. The registry reports an analysis using Fisher Exact, but it does not give enough detail to reconstruct all aspects of the sponsor’s analysis.

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.

6. Primary Endpoint

The registry lists the primary outcome as Need for Additional Uterotonic Medications, measured over 24 hours.

The primary endpoint is the percentage of participants who needed additional uterotonic medication within 24 hours. According to the registry definition, the surgeon requested additional agents based on clinical findings during surgery, such as uterine atony or blood loss of at least 1000 mL. Additional oxytocin was also counted as an additional uterotonic intervention for the analysis.

This endpoint is useful because it captures a treatment decision made in response to clinical findings. It can therefore reflect whether clinicians judged that additional uterotonic support was needed. It is not a direct measure of blood loss alone, and the endpoint does not identify which clinical finding prompted each request. The registry record does not report the individual reasons for additional medication or the specific agents used beyond the note about oxytocin.

For the posted results, the outcome is expressed as a percentage rather than a continuous quantity. That makes the main comparison a comparison of event proportions between the randomized groups. The observed percentages describe how often the defined intervention occurred in each arm; they do not, by themselves, establish why the groups differed. Interpretation also depends on the trial’s population, endpoint definition, precision, and completeness of reporting.

7. Results Posted in the Registry

• Folic Acid: 40.0% (24/60) versus 10.0% (6/60) on control; risk difference 30.0 percentage points (95% CI 15.5 to 44.5), risk ratio 4.00 (1.76–9.08); unadjusted two-proportion z-test p = <0.001.

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.

Uterine Atony

• 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:
  • Folic Acid: 25.0% (15/60) versus 8.3% (5/60) on control; risk difference 16.7 percentage points (95% CI 3.7 to 29.7), risk ratio 3.00 (1.16–7.73); unadjusted two-proportion z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Folic Acid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Postpartum Hemorrhage

• 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:
  • Folic Acid: 20.0% (12/60) versus 6.7% (4/60) on control; risk difference 13.3 percentage points (95% CI 1.4 to 25.3), risk ratio 3.00 (1.03–8.78); unadjusted two-proportion z-test p = 0.032.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Folic Acid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes concern uterine atony, postpartum hemorrhage and blood loss. For the outcomes with posted arm percentages and comparisons, the overall pattern is directionally consistent with the primary endpoint: the recorded event percentages are lower in the misoprostol arm than in the folic-acid arm. This coherence can make the pattern of results easier to understand, because the endpoints relate to the clinical events and interventions that motivated the trial.

These outcomes are not identical to the primary endpoint. Uterine atony and postpartum hemorrhage describe clinical events, while the primary endpoint records a request for additional uterotonic medication. A consistent direction across related measures does not establish that one outcome caused another, or that the secondary findings independently verify the primary result. The registry lists blood loss as a secondary outcome, but the posted secondary data do not include a corresponding numerical result in the record; its result is not reported in the registry record.

The secondary comparisons are unadjusted in the recalculation, and the registry does not report a correction for testing multiple outcomes. When several outcomes are examined, the chance of obtaining at least one apparently notable result can increase. This is why unadjusted secondary p-values generally carry less weight than a clearly prespecified primary analysis, particularly when the testing plan and multiplicity strategy are not reported.

The sponsor-reported p-values and recalculated values are not fully aligned. The discrepancy flagged for the primary comparison reinforces the need to distinguish sponsor analyses from summary-statistic recalculations for the secondary endpoints as well. The secondary pattern is descriptive and potentially supportive, but it should be interpreted alongside uncertainty, multiplicity, and the incomplete reporting of the analysis plan.

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

• Uterine Atony
• Postpartum Hemorrhage
• Blood Loss

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary: each participant either did or did not have the recorded event, defined as needing additional uterotonic medication. The arm percentages describe the proportion with an event in each group. For a binary endpoint, an absolute risk difference is one way to express the contrast between groups. In the recalculation, the comparison is framed as the folic-acid percentage minus the misoprostol percentage, so a positive value means the event percentage was higher in the folic-acid arm.

What does the risk difference tell us?

The recalculated risk difference is an absolute contrast in the observed event proportions. It is expressed on the probability scale, rather than as a relative comparison. The reported interval gives a range of values compatible with the data under the calculation’s assumptions. An interval that does not include no difference indicates that the data are inconsistent with that particular null value at the confidence level used. It does not establish that the estimate is free from bias, nor does it address whether the trial population represents other settings.

The risk difference is recalculated from the posted group-level event counts and denominators. It is unadjusted: it does not account for covariates or other features of the participants. The registry does not report an adjusted effect estimate for the primary endpoint. The recalculation is therefore a simple comparison of the posted summaries, not a substitute for a more detailed participant-level analysis.

Why is Fisher Exact reported?

The registry identifies Fisher Exact as the method for the sponsor-reported analyses. This test evaluates evidence of an association between group assignment and a binary outcome using the observed counts. It is commonly used for categorical data, including situations with relatively small event counts. The registry reports p-values from that method but does not provide the full analysis specification, such as whether any additional adjustments or analysis-population rules were applied.

A p-value describes how compatible the observed data are with a specified null hypothesis under the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an effect. Nor does a small p-value alone convey how precisely the effect has been estimated. For that, the size of the estimated contrast and its confidence interval are important.

Why are the recalculated and sponsor results different?

The posted summaries permit an unadjusted recalculation, while the registry’s own analysis is reported as Fisher Exact. The recalculated primary p-value is <0.001, whereas the registry reports p <0.01. The record flags a discrepancy. The sponsor’s own analysis takes precedence; the recalculation is useful as a check based on the posted summary statistics, but it should not be presented as replacing the sponsor’s result. The registry does not report enough detail to establish why the p-values differ.

For uterine atony and postpartum hemorrhage, the registry also gives Fisher Exact p-values alongside recalculated unadjusted results. The same distinction applies: the sponsor’s reported result is the trial’s own analysis, while the recalculation is based on the posted counts and is not adjusted. Differences between these values should not be resolved by selecting whichever is more favorable. They signal that the analysis details and the reported summaries need to be considered together.

What does a confidence interval contribute?

A confidence interval communicates uncertainty in an estimate, not just whether a test crosses a significance threshold. Its endpoints indicate the range of effect sizes compatible with the data under the calculation and its assumptions. A relatively broad interval leaves more uncertainty about the magnitude; a narrower interval gives greater precision for that estimate. The interval does not capture every source of uncertainty, such as selection bias, misclassification, missing data, or limitations in generalizability.

The primary recalculated interval is for the unadjusted risk difference. The registry’s reported primary analysis supplies a p-value but no sponsor-reported effect estimate or confidence interval. This distinction matters: the p-value alone cannot replace an estimate of the between-group difference or its precision.

Why might over-dispersion matter in other settings?

Over-dispersion is general statistical terminology for variation greater than a model expects. It can make standard errors too small if a model assumes less variability than the data contain, which can make confidence intervals too narrow and tests too optimistic. This trial’s reported binary summaries do not provide evidence that an over-dispersed model was used or needed. The point is general: model assumptions should match the type and variability of the data, and the registry does not report a model-based analysis for these binary outcomes.

The registry lists four outcome measures and four analyses, with three secondary outcomes posted. It does not report whether the analyses were prespecified in the same form, whether adjustments were made for multiple comparisons, or how missing observations were handled. Those omissions limit assessment of the complete statistical strategy. They also mean the posted p-values should be interpreted in context rather than as a comprehensive account of all planned or performed analyses.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. The recalculated primary risk difference is 0.3, with a 95% confidence interval from 0.155 to 0.445. This interval remains on the side of a higher event proportion in the folic-acid arm, given the stated direction of comparison. It still spans a range of possible magnitudes, so the estimate should not be read as an exact value.

The reported sponsor analysis does not include a primary effect estimate or confidence interval in the registry record. Its p-value, p <0.01, gives evidence against the test’s null hypothesis but does not communicate the size of the estimated difference or its uncertainty. The recalculated interval supplies that information for the unadjusted summary comparison; because the record flags a discrepancy, it should not be mistaken for the sponsor’s own interval.

Confidence intervals reflect sampling uncertainty under the calculation’s assumptions. They do not account for every limitation, including possible outcome misclassification, incomplete follow-up, or unreported analysis choices. The registry record does not describe missing-data handling or give a detailed analysis population. Precision in the numerical estimate therefore should be distinguished from confidence in all aspects of trial conduct and reporting.

The secondary endpoints also have recalculated intervals, but the registry’s sponsor analyses provide p-values without corresponding effect intervals. Their numerical precision does not resolve the separate concern that several outcomes were assessed and no multiplicity procedure is reported. Taken together, the estimates describe the posted data, while uncertainty about analysis choices and the full set of comparisons remains.

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 sample-size figures are planning illustrations based on the observed effect, not the original trial design. For these non-time-to-event outcomes, the figures are participants per arm, not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect as the effect to detect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% column describes a higher target chance of detection and therefore gives a larger planning requirement for the same assumed effect. These are design calculations, not descriptions of how likely the completed trial was to find an effect after its results were known.

The rows that plan for 100%, 75% and 50% of the observed effect let readers consider progressively smaller target effects. Smaller effects are harder to distinguish from chance variation, so they require more participants under the same assumptions. For example, the primary-outcome illustration lists 32 participants per arm for 80% power when planning for 100% of the observed effect, and 100 participants per arm when planning for 50% of that effect. These examples describe the illustration only, not the trial’s original recruitment rationale.

The registry record does not report the trial’s original sample-size assumptions or justification. These figures are not observed power: observed power is not a useful substitute for interpreting the effect estimate and its uncertainty after results are available. The planning figures instead show how assumptions about effect size and desired power influence a prospective sample-size calculation.

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 = 0.100; treatment proportion p₁ = 0.400; average p̄ = 0.250.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6124 = 1.2002.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5745 = 0.4835.
4. n = (1.2002 + 0.4835)² / (0.3000)² = 31.5, rounded up to 32 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 <- 0.1                          # control proportion
p1 <- 0.4                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1733329)
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 = 32 (80% power), 42 (90% power)
 75% of observed effect: n per arm = 51 (80% power), 68 (90% power)
 50% of observed effect: n per arm = 100 (80% power), 133 (90% power)
power.prop.test: 31.5 
Simulated power at n = 32 per arm: 0.832 (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 reports Fisher Exact as the sponsor’s method for the primary comparison and gives p <0.01. A recalculation from the posted group summaries gives an unadjusted p-value of <0.001 and an unadjusted risk difference of 0.3, with a 95% confidence interval from 0.155 to 0.445. The record flags a discrepancy between the sponsor result and the recalculation. For the trial’s reported inferential result, the sponsor’s own analysis takes precedence.

The recalculation remains useful as a transparent check of the posted percentages and event counts. It is not a reconstruction of every possible choice in the sponsor’s analysis, because the registry does not describe the full analysis plan, analysis population, or any additional procedures. The difference in p-values cannot be explained from the registry record, and it should not be treated as evidence that one analysis is necessarily erroneous.

For the secondary outcomes, sponsor-reported Fisher Exact p-values are also listed, alongside recalculated unadjusted comparisons. The same interpretive distinction applies. The sponsor’s p-values are the results attributed to the trial analysis; the recalculated estimates are simple summary-statistic comparisons. Neither type of p-value conveys the effect’s practical importance by itself, and the lack of a reported multiplicity approach limits the weight placed on secondary significance tests.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists secondary endpoints, but does not report a multiplicity adjustment or a hierarchy for interpreting the tests. Multiplicity matters when several hypotheses are assessed: even if each test uses a conventional threshold, the overall chance of at least one false-positive finding can rise as more comparisons are considered. An adjustment or prespecified testing sequence can help control that risk. Whether either was used in this trial is not reported in the registry record.

The registry lists four outcome measures and four analyses, and three secondary outcomes are posted. It does not explain how the complete set of measures relates to the posted results, whether outcomes were selected for reporting after analysis, or whether any outcomes were omitted. These unknowns do not prove selective reporting, but they limit a reader’s ability to assess the full testing burden and the status of each comparison.

Missing-data procedures are also not reported in the registry record. It does not state how participants with unavailable endpoint data were handled, whether any imputation was used, or whether follow-up was complete for each outcome. The posted arm denominators are listed, but the registry does not describe whether they represent all randomized participants or an analysis subset. The analysis population, including whether an intention-to-treat approach was used, is not reported in the registry record.

Random allocation is recorded, but the registry does not provide enough detail to assess allocation concealment, implementation, or deviations from assigned treatment. It also does not report whether sensitivity analyses were conducted. Those details matter because choices about exclusions, missing outcomes and analysis populations can affect estimates and p-values. The absence of such information is a reporting limitation, not proof that the trial failed to address these issues.

Given these gaps, the primary result deserves the clearest emphasis, while secondary findings should remain supportive and exploratory in interpretation. The record’s sponsor-reported analysis should be distinguished from recalculated unadjusted results, and neither resolves the unanswered questions about multiplicity and missing data.

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 registry reports serious adverse events in 0 of 60 participants in the misoprostol arm and 0 of 60 in the folic-acid arm. It also reports other adverse events in 0 of 60 participants in each arm. These entries indicate that no events in those categories were recorded in the posted safety data for the stated groups.

Zero reported events should not be interpreted as proof that no adverse effects can occur. The registry does not provide a detailed description of how adverse events were collected, how long safety follow-up continued, or which events counted as serious or other adverse events. The deaths fields are not populated, and deaths are not reported in the registry record. No serious adverse-event terms are listed.

Safety interpretation is therefore limited to what the record reports. The entries do not establish that the treatments have equivalent safety, nor do they quantify rare risks. They describe the recorded event counts within this trial and should be read with the reporting and follow-up details that are available.

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

The results describe a randomized comparison in women with risk factors for uterine atony who underwent cesarean delivery. The posted primary outcome percentages are lower in the misoprostol arm than in the folic-acid arm, and the recalculated unadjusted comparison indicates a difference between those recorded proportions. The sponsor’s reported Fisher Exact result is p <0.01; because the record flags a discrepancy with the recalculation, the sponsor’s analysis takes precedence as the trial’s own inferential result.

This does not establish that the observed difference will occur in every population or clinical setting. The trial description is specific to women with risk factors for uterine atony undergoing cesarean delivery, and the registry does not detail the risk factors or provide a broad description of other eligibility criteria. Generalizability beyond the recorded population is therefore uncertain.

The primary endpoint is a request for additional medication, not a direct measure of blood loss or a complete measure of postpartum health. The secondary outcomes offer related clinical information, but they do not remove the limitations of the primary endpoint or the unreported multiplicity approach. The results also do not establish the mechanism behind the observed pattern.

The registry’s reported safety entries contain no recorded serious or other adverse events in either arm, but the available information is insufficient to conclude that there is no safety risk. Follow-up and event-collection details are not reported. Likewise, missing-data handling, analysis populations and the original sample-size rationale are not reported.

Overall, the posted results are evidence about this specific trial comparison and its recorded outcomes. They are not, on their own, a recommendation for care, a guarantee of effect, or a complete account of benefits and harms. The interpretation depends on the study design, endpoint definitions, precision, and gaps in registry reporting.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, its uncertainty and the analysis method should be read together. A difference in percentages gives an intuitive description of the observed groups, while a confidence interval indicates how much uncertainty remains about the size of that difference. A p-value addresses compatibility with a null hypothesis, but does not tell readers whether the effect is important or precisely estimated.

It also demonstrates the distinction between a sponsor-reported analysis and a recalculation from posted summary statistics. The registry reports Fisher Exact results, while recalculated unadjusted comparisons are available from the displayed counts and denominators. Where the record flags a discrepancy, the sponsor’s analysis takes precedence, and the discrepancy itself is a reason to avoid treating the recalculation as a replacement for the trial report.

The related secondary outcomes offer context, but multiple testing and incomplete reporting affect how strongly they can support the primary finding. Without a reported multiplicity strategy, the secondary p-values should not be interpreted as if each were the sole planned test. Similarly, the absence of detail on missing data and analysis populations limits confidence about whether all randomized participants contributed to each result.

Finally, the sample-size illustrations show how planned requirements depend on the target effect and desired power. They are not evidence about the trial’s original design rationale and are not observed power. Keeping these concepts separate helps readers distinguish what the trial recorded, what a recalculation estimates, and what a planning exercise can say about future study design.

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 registry record leaves several trial-specific questions unanswered. Although it identifies randomization and double masking, it does not describe the randomization sequence, allocation concealment, masking procedures, or whether masking was maintained. The summary calls the study placebo-controlled, while the comparator arm is described as folic acid. The record does not explain this inconsistency.

The enrollment field records 123, while each arm description lists n=60. The registry does not reconcile these entries or explain whether the enrollment figure refers to a different stage or definition. The original sample-size justification is not reported, so the planning illustrations based on observed effects should not be mistaken for the trial’s prospective design calculation.

The primary endpoint depends on a clinical request for additional medication based on findings during surgery. The registry definition includes additional oxytocin, but does not report the specific reasons for each request, the number of requests by agent, or whether decision-making was standardized across clinicians. The outcome is therefore a measure of intervention under the stated definition, not a direct measure of blood loss alone.

The registry does not report the full analysis plan, multiplicity handling, missing-data methods, analysis populations, or sensitivity analyses. It also does not provide sponsor-estimated confidence intervals for the primary comparison. A discrepancy is flagged between the sponsor’s primary p-value and the recalculated unadjusted result, but the record does not explain its source.

Safety reporting is limited to the posted counts, without detailed adverse-event definitions or follow-up information. The registry also does not provide a numerical result for the listed blood-loss secondary outcome. These limitations constrain assessment of precision, robustness, and the completeness of the reported outcome set.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Buccal Misoprostol During Cesarean Section for Preventing Postpartum Hemorrhage — NCT01733329.
• Registry record last updated 2018-10-11; status last verified 2018-10.
• Results first posted 2014-03-31.
• 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 describes a completed Phase 4, randomized, double-blind, parallel-group trial of buccal misoprostol during cesarean delivery in women with risk factors for uterine atony. The primary endpoint was the need for additional uterotonic medication within 24 hours. The comparator arm is described as receiving buccal folic acid, although the brief summary calls the study placebo-controlled.

The posted primary percentages are 10.0% for misoprostol and 40.0% for folic acid. The registry reports a Fisher Exact p-value of <0.01, while the recalculated unadjusted comparison differs; the sponsor’s analysis takes precedence. Secondary outcomes include uterine atony, postpartum hemorrhage and blood loss. The record reports no serious or other adverse events in either arm, but safety and analysis details are limited.

The registry does not report the original sample-size rationale, multiplicity approach, missing-data handling, or analysis populations. The posted results should therefore be interpreted as a specific randomized comparison with important reporting limitations.