Low-Dose Versus High-Dose Oxytocin Dosing for Induction and Augmentation of Labor: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Low-Dose Versus High-Dose Oxytocin Dosing for Induction and Augmentation of Labor (NCT05782816), a randomized phase 4 study. The primary outcome is Time to Delivery.

2. Clinical Question

The registry describes a randomized, single-masked, parallel-group trial. The record is marked completed and identifies the study as Phase 4. It does not report what parties were masked, how randomization was implemented, or whether the analysis followed the randomized assignments. Those details are important for interpreting how well the comparison protects against bias, but they are not reported in the registry record.

3. Trial Design

The trial compared two oxytocin infusion strategies in a randomized, parallel-group design. Participants were assigned to low-dose or high-dose oxytocin. Under the low-dose protocol, the infusion started at 2 milli-units/min and increased by 2 milli-units/min every 20 minutes. Under the high-dose protocol, it started at 6 milli-units/min and increased by 6 milli-units/min every 20 minutes. Both protocols specified a maximum rate of 40 milli-units/min. The registry describes a controlled infusion pump delivered through a proximal port on a peripheral IV line.

The study is listed as single-masked, but the identity of the masked party and the procedures used to maintain masking are not reported in the registry record. The record identifies random allocation and a parallel model; it does not describe the sequence-generation method, allocation concealment, stratification, or any other design features that might affect the comparability of groups.

Enrollment is listed as 170. For the primary endpoint, the posted arm summaries include 84 participants in the low-dose group and 85 in the high-dose group. The primary endpoint is time to delivery, expressed as a mean in minutes with standard deviations. Its stated timeframe is through delivery, on average 24 hours. The record is marked completed, with a start date of 2023-04-17 and a primary completion date of 2024-12-31.

The registry lists 13 outcome measures and identifies 12 secondary outcomes as posted. Quantitative results are available for three secondary outcomes in the record: primary cesarean delivery, uterine tachysystole and postpartum hemorrhage. Although the registry also names other outcomes, their results are not reported in the registry record. The original sample-size justification, planned statistical analysis, analysis populations, handling of missing observations and any interim analyses are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

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 Time to Delivery, measured over Through delivery, on average 24 hours.

The primary endpoint is time from induction to delivery, described as the induction-to-delivery time interval. It is measured in minutes and summarized as a mean with a standard deviation for each randomized group. The stated observation period is through delivery, on average 24 hours.

This endpoint captures the duration of the induction-to-delivery process as a continuous measure. Comparing group means addresses whether the average interval differed between participants assigned to the high-dose and low-dose protocols. A mean is useful for describing the overall level of a continuous outcome, while the standard deviation describes how much individual observed times vary around that group mean. The mean difference does not describe every participant's experience, and it may not reveal the distribution's shape or whether a small number of unusually long intervals influence the average.

The posted mean was 1042.0 minutes in the low-dose group and 971.1 minutes in the high-dose group. The estimated high-dose-minus-low-dose mean difference was -70.7 minutes. These are group summaries and an estimated contrast, not a statement about what would happen to a particular participant. The endpoint is also only one part of the trial's stated questions: delivery mode and maternal and neonatal outcomes are separate outcomes and cannot be inferred from the induction-to-delivery interval alone.

The registry does not report further operational details about how the start and end of the interval were defined, whether all randomized participants contributed to this endpoint, or how incomplete observations were handled. Those details are not reported in the registry record.

7. Results Posted in the Registry

• High Dose Oxytocin: mean 971.10 versus 1,042 on control; difference -70.70 (95% CI -230.03 to 88.63), standardized effect d = -0.13; z-test p = 0.384.

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.

Rate of Primary Cesarean Delivery

• 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:
  • High Dose Oxytocin: 1.2% (1/85) versus 29.8% (25/84) on control; risk difference -28.6 percentage points (95% CI -38.6 to -18.5), risk ratio 0.04 (0.01–0.29); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for High Dose Oxytocin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Rate of Uterine Tachysystole

• 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:
  • High Dose Oxytocin: 25.9% (22/85) versus 17.9% (15/84) on control; risk difference 8.0 percentage points (95% CI -4.4 to 20.4), risk ratio 1.45 (0.81–2.60); unadjusted two-proportion z-test p = 0.207.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Oxytocin and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Postpartum Hemorrhage

• 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:
  • High Dose Oxytocin: 4.7% (4/85) versus 1.2% (1/84) on control; risk difference 3.5 percentage points (95% CI -1.5 to 8.6), risk ratio 3.95 (0.45–34.64); unadjusted two-proportion z-test p = 0.177.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Oxytocin and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes do not form a uniform pattern. The primary cesarean delivery comparison has a risk-difference interval that lies below no difference, while the uterine tachysystole and postpartum hemorrhage intervals include values in both directions. Their unadjusted p-values likewise differ in how strongly they distinguish the observed data from a no-difference model. These outcomes address distinct aspects of delivery and maternal experience; they should not be combined into a single overall conclusion.

The secondary outcomes complement but do not replace the primary induction-to-delivery comparison. A difference in delivery mode would not, by itself, establish a difference in average time to delivery, and the primary mean result cannot determine whether other maternal outcomes differ. Each endpoint has its own definition, count or measurement scale, and uncertainty. The overall interpretation should therefore retain the primary endpoint as the trial's stated primary question while treating secondary patterns as additional, outcome-specific evidence.

Unadjusted secondary results carry less weight for confirmatory conclusions when many outcomes are assessed. Without a prespecified testing hierarchy or multiplicity procedure, a low unadjusted p-value may overstate the strength of evidence if it is considered in isolation from the full set of analyses. The registry does not report a multiplicity plan. It also does not report analysis methods for the posted outcomes or identify which results were designated as confirmatory.

The registry lists 12 secondary outcomes as posted, but quantitative results are available for only three in the record. The remaining listed secondary results are not reported in the registry record. This limits any assessment of the full secondary-outcome pattern and makes it important not to treat the available results as a complete account of every maternal and neonatal question raised by the trial.

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

• Mode of Delivery
• Rate of Primary Cesarean Delivery
• Maximum Dose of Oxytocin Infusion
• Rate of Uterine Tachysystole
• Number of Participants With Postpartum Hemorrhage
• Rate of Placental Abruption
• Number of Participants With Nausea/Vomiting Requiring Antiemetics and Diarrhea
• Rate of Maternal Infection (Endometritis, Chorioamnionitis)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: elapsed time to delivery, measured in minutes. The registry summarizes each arm with a mean and standard deviation. A mean difference compares those group averages. In the posted comparison, the contrast is high dose minus low dose, so a negative estimate corresponds to a lower observed mean in the high-dose group. The estimated contrast was -70.7 minutes. The posted standard deviations were 537.5 minutes for low dose and 519.0 minutes for high dose, reflecting appreciable variation among individual recorded times around their respective means.

A confidence interval describes a range of estimates compatible with the observed data under the method's assumptions. It is not a range containing a known proportion of individual participant outcomes, and it is not the probability that the true effect lies within the particular interval. The primary interval, -230.0 to 88.63 minutes, spans effects in both directions. Its breadth matters: the point estimate is not sufficiently precise to establish a narrow range of plausible mean differences. The unadjusted p-value of 0.384 measures how unusual data at least as incompatible with a no-difference model would be under that model and the test's assumptions. It does not measure the probability that the null hypothesis is true.

For binary outcomes, the record reports counts and risk differences. A risk difference contrasts the observed proportions in the two groups; negative values in these comparisons indicate a lower observed proportion in the high-dose group. For primary cesarean delivery, the estimated risk difference was -0.286 and its interval was -0.386 to -0.185. The unadjusted p-value was <0.001. For uterine tachysystole, the estimate was 0.080 with an interval from -0.044 to 0.204 and p = 0.207. For postpartum hemorrhage, the estimate was 0.035 with an interval from -0.015 to 0.086 and p = 0.177. An interval that spans no difference indicates that the data do not sharply distinguish an increase from a decrease under the reported interval method.

The registry also gives relative measures for these binary comparisons, including risk ratios and odds ratios. Such measures express contrasts on different scales from risk differences. Relative measures can look especially large or unstable when events are uncommon, and the intervals for the postpartum hemorrhage relative measures are wide. The absolute counts and risk differences help retain the scale of the observed data. No single scale answers every interpretive question.

All secondary p-values are explicitly unadjusted. When several outcomes are examined, the chance of at least one apparently unusual result can increase if no adjustment or testing hierarchy is used. The record does not report whether the secondary outcomes were prespecified as confirmatory, whether any multiplicity correction was planned, or which analysis methods generated the reported intervals and p-values. The registry lists no reported analyses. Consequently, the displayed estimates should be treated as registry-posted comparisons, not as a fully documented statistical analysis plan.

General statistical context: standard deviations describe spread among observations, whereas standard errors describe uncertainty in an estimated quantity such as a mean. A confidence interval is commonly constructed from an estimate and its standard error, with a method chosen to suit the outcome and design. The exact methods used for the posted comparisons are not reported in the registry record. For binary outcomes with sparse events, approximate methods can be sensitive to small changes in counts; the record does not describe any alternative or exact procedures used to address this issue.

Over-dispersion is a general concern when count data vary more than a chosen model expects, because standard errors can then be too small and intervals too narrow. The primary endpoint is reported as a continuous measure, not a count model, and the record does not report an over-dispersion assessment. Likewise, the record does not give the distribution of individual delivery times, diagnostics, transformations, covariate adjustments, or subgroup analyses. Those omissions prevent assessment of model fit or whether adjusted analyses would materially differ.

The sample-size figures are planning illustrations based on the observed effects, not a description of the trial's original design calculations. General power calculations estimate how often a design would detect an assumed effect under specified assumptions if repeated. They do not describe the probability that the observed result is true, and they should not be used as retrospective evidence that a nonsignificant comparison had adequate power. The registry's original sample-size justification and statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is reflected in the width of an uncertainty interval: narrower intervals usually indicate a more precise estimate, while wider intervals leave more plausible values open. The primary mean difference was -70.7 minutes, with an interval from -230.0 to 88.63 minutes. This interval includes a range extending from a lower average time in the high-dose arm to a higher average time. The estimated direction is therefore uncertain, and the interval does not support a tightly bounded estimate of the mean contrast.

For primary cesarean delivery, the risk-difference interval was -0.386 to -0.185. In contrast, the intervals for uterine tachysystole (-0.044 to 0.204) and postpartum hemorrhage (-0.015 to 0.086) include no difference and permit effects in either direction. These intervals should be interpreted alongside their event counts. The postpartum hemorrhage counts were 1 and 4, so its estimate is based on few recorded events and is correspondingly uncertain; the relative-effect intervals are also broad.

A confidence interval is not a guarantee that the true value lies in its limits, nor does an interval spanning no difference prove there is no effect. It describes uncertainty under the interval method and assumptions. The registry does not report the exact interval-construction methods, missing-data procedures, or analysis population, so precision cannot be assessed fully from the record alone.

For the continuous endpoint, the posted standard deviations were large relative to the magnitude of the estimated mean difference. That pattern is consistent with substantial variability in individual delivery times, but group-level summaries do not reveal the shape of the underlying distributions. The interval is more informative about uncertainty in the mean contrast than the standard deviations alone. It remains important not to mistake a point estimate for a precise or certain result.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the binary outcomes and the continuous mean comparison; they are not total event counts. The registry's planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial's original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm that the calculation estimates would be needed for an 80% chance of detecting the assumed effect under those planning assumptions. The 90% power column gives the corresponding per-arm number for a 90% chance. These are design calculations for hypothetical future studies based on the observed effect and its stated fractions. They are not observed power for this completed trial.

Each row changes the assumed target from the full observed effect to 75% or 50% of that effect. A smaller effect is harder to distinguish from random variation, so the planning calculation requires more participants per arm to reach the same target power. For example, the primary endpoint's listed requirement rises from 877 participants per arm for 80% power at 100% of the observed effect to 3,506 at 50% of the observed effect. These figures illustrate how strongly planning needs depend on the effect assumed; they should not be read as a recommendation or as a re-creation of the trial's design.

The calculations are based on observed effects, which can be unstable, especially for outcomes with few events. They also rely on the stated assumptions and do not incorporate design details not reported in the registry record. The planning values therefore describe hypothetical scenarios rather than the precision or success of the completed trial.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -70.700; pooled standard deviation σ = 528.276.
2. n = 2 × (1.96 + 0.842)² × 528.276² / -70.700² = 876.4, rounded up to 877 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -70.6999999999999                      # observed difference in means
sigma <- 528.275596906979                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

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

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(5782816)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 877 (80% power), 1,174 (90% power)
 75% of observed effect: n per arm = 1,559 (80% power), 2,086 (90% power)
 50% of observed effect: n per arm = 3,506 (80% power), 4,694 (90% power)
power.t.test: 877.4 
Simulated power at n = 877 per arm: 0.802 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry names multiple secondary outcomes, including mode of delivery, maximum oxytocin dose, uterine tachysystole, postpartum hemorrhage, placental abruption, gastrointestinal symptoms requiring treatment, and maternal infection. It also states broader questions about maternal and neonatal outcomes. Testing several outcomes creates a multiplicity issue: even when each individual test uses a conventional threshold, repeated testing can make at least one apparently notable finding more likely by chance. General approaches include specifying a primary outcome hierarchy, adjusting inference for multiple tests, or clearly labeling secondary findings as exploratory.

The registry record does not report a multiplicity adjustment, testing hierarchy, or distinction between confirmatory and exploratory secondary analyses. The posted secondary p-values are unadjusted. The primary endpoint has a single stated role in the record, but the details of the statistical plan and any prespecified interpretation rules are not reported in the registry record. Accordingly, secondary p-values should not be treated as though they were adjusted or protected by a stated hierarchy.

The record does not report how missing observations were handled, whether outcome data were complete for all randomized participants, or whether any participants were excluded from particular analyses. It also does not report an intention-to-treat, per-protocol, or other analysis population. The reported arm denominators for the primary endpoint and secondary outcomes are available, but those counts alone do not explain how the analysis population was defined or whether all randomized participants were included.

There is no reported account of imputation, sensitivity analyses for missing data, or reasons for missing outcomes. For a labor and delivery study, the registry's endpoint timeframe is through delivery, but the record does not describe how transfer, withdrawal, or other incomplete follow-up situations were treated. These are not claims that such issues occurred; the relevant procedures are simply not reported in the registry record.

The registry lists no reported analyses. It does not describe interim analyses, stopping rules, covariate adjustment, subgroup analyses, or the exact methods used to obtain the reported confidence intervals and p-values. These gaps limit reproducibility and make it difficult to determine whether the posted comparisons follow an analysis plan established before outcomes were examined.

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 0% reporting threshold.

The registry reports no serious adverse events and no deaths in either group. The serious-adverse-event risk groups were 84 for low-dose oxytocin and 85 for high-dose oxytocin; the serious-event counts were zero in both groups. The registry also reports zero other adverse events in each group, with 84 and 85 participants at risk, respectively.

These counts describe the adverse-event information entered in the registry record for the stated risk groups. They do not establish that no adverse events of any kind occurred beyond what was recorded, and they do not show that the protocols have identical safety profiles. With no recorded serious events, the data provide limited information about the frequency of uncommon harms. The record does not provide further details on event definitions, ascertainment, follow-up completeness, or the severity and nature of other reported events. The absence of listed serious events should therefore be read as a registry result, not as proof of no risk.

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

The results describe a randomized comparison of two infusion protocols and report a mean induction-to-delivery interval for each group. The estimated mean difference favored a shorter observed interval in the high-dose group at the point-estimate level, but its confidence interval spans both lower and higher mean times. The primary comparison therefore remains imprecise, and the unadjusted p-value does not establish a clear difference under the posted analysis.

The secondary results provide separate, endpoint-specific observations. The primary cesarean delivery comparison has a notably different pattern from the primary time endpoint, while the intervals for uterine tachysystole and postpartum hemorrhage allow effects in either direction. These findings do not combine into a single measure of overall benefit or harm. Quantitative results for other listed secondary outcomes are not reported in the registry record, and the registry does not state how multiple outcomes were to be interpreted together.

A randomized design is intended to support fair comparison between assigned groups, but the record does not include enough methodological detail to assess sequence generation, allocation concealment, masking procedures, missing data, or the analysis population. Randomization does not remove uncertainty due to limited information, outcome measurement, or incomplete reporting.

The results do not establish what would happen to an individual participant, and they do not demonstrate equivalence between protocols. They also do not answer every question about delivery mode, maternal outcomes, or neonatal outcomes. The primary endpoint addresses time to delivery; separate data and analyses are needed to evaluate other outcomes. The small number of recorded events for some secondary outcomes and their unadjusted status further limit how confidently those results can be generalized.

The appropriate reading is descriptive and cautious: the record presents group-level estimates with different degrees of precision, and several details needed for a complete assessment are not reported in the registry record. No clinical recommendation follows from these statistics alone.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized clinical comparison is interpreted through both the estimated effect and its uncertainty. The primary point estimate is straightforward to describe, but its interval is broad enough to leave the direction of the underlying mean contrast unresolved. Reporting the point estimate without the interval would give an incomplete impression of what the data establish.

The record also illustrates how different endpoints can tell different statistical stories. Time to delivery is a continuous measure summarized by means, whereas delivery mode and the other posted secondary outcomes are represented by event counts and risk differences. Their scales, event frequencies and precision differ. A striking contrast on one secondary outcome should not be substituted for the primary question, and a primary result cannot stand in for all maternal or neonatal outcomes.

Multiplicity is relevant because the registry lists many outcomes but does not report a testing hierarchy or adjustment. Unadjusted results can be useful for describing the data, but their evidential weight depends on whether they were planned as confirmatory and how they relate to the full set of analyses. That context is not reported in the registry record.

Finally, the sample-size illustrations show how planning conclusions depend on the effect size assumed. Smaller target effects require more participants per arm under the stated assumptions. Because these calculations use the observed effects and are not the original trial design justification, they cannot explain why the trial enrolled the recorded number of participants or establish whether its design was adequate for every outcome.

18. Limitations

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

Several trial-specific limitations arise from the information available in the registry record. Although the study is described as randomized and single-masked, the record does not identify the masked party or explain the randomization and allocation-concealment procedures. It also does not provide detailed eligibility criteria beyond the stated focus on nulliparous women undergoing induction or augmentation of labor. This limits assessment of how closely the enrolled population can be characterized.

The primary endpoint is summarized with group means and standard deviations, but the record does not provide individual-level distributions, medians, ranges, or details about influential observations. The endpoint definition does not specify further operational rules for measuring the start and end of the interval. The record also does not describe missing observations, analysis populations, or whether adjustment for baseline factors was planned.

Quantitative results are available for only three of the listed secondary outcomes. This leaves the broader set of maternal and neonatal questions incompletely represented in the posted results. The secondary comparisons are unadjusted, and no multiplicity plan is reported. Sparse event counts for some outcomes also mean that the estimates can be unstable and their uncertainty substantial.

The original sample-size justification, the prespecified statistical plan, interim analyses, and exact analysis methods are not reported in the registry record. The planning illustrations based on observed effects cannot fill those gaps. Nor do the reported absence of serious adverse events and deaths establish that uncommon harms are absent; the record does not detail event ascertainment or follow-up completeness.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Low-Dose Versus High-Dose Oxytocin Dosing for Induction and Augmentation of Labor — NCT05782816.
• Registry record last updated 2026-01-09; status last verified 2025-12.
• Results first posted 2026-01-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes NCT05782816, a completed Phase 4, randomized, single-masked, parallel-group trial sponsored by The University of Texas Medical Branch, Galveston. It compared low-dose and high-dose oxytocin infusion protocols for induction and augmentation of labor in nulliparous women. Enrollment is listed as 170, and the primary endpoint is mean time from induction to delivery in minutes.

The observed mean was 1042.0 minutes for low dose and 971.1 minutes for high dose. The estimated mean difference was -70.7 minutes, with a confidence interval from -230.0 to 88.63 and an unadjusted p-value of 0.384. Posted secondary results cover primary cesarean delivery, uterine tachysystole and postpartum hemorrhage; other listed secondary results are not reported in the registry record.

The record reports zero serious adverse events and zero deaths in both groups. It does not report the original sample-size justification, detailed statistical plan, multiplicity strategy, missing-data procedures, or analysis populations. Interpretation should therefore distinguish the posted group summaries from conclusions that would require those additional details.