Oral Nifedipine Versus Oral Labetalol: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oral Nifedipine Versus Oral Labetalol (NCT02168309), a randomized na study. The primary outcome is Time (Hours) to Attain Sustained Blood Pressure Goal After Treatment Initiated With Antihypertensive Medication.

2. Clinical Question

The comparison is framed as a superiority question: the study summary states a hypothesis that extended-release oral nifedipine would be superior to oral labetalol for achieving the blood pressure goal postpartum. That statement describes the study’s hypothesis, not a conclusion about the posted results. The record does not specify the numerical blood pressure threshold that defined the goal, how sustained control was operationalized, or what counted as the starting point for measuring time beyond treatment initiation.

For interpretation, the primary outcome is a continuous measure, reported as a mean and standard deviation in each arm. The posted comparison expresses the mean difference as nifedipine minus labetalol. A positive value therefore indicates a higher mean in the nifedipine arm for this outcome, while the confidence interval and p-value describe uncertainty and evidence against a no-difference comparison. Neither measure alone establishes that a medication is superior.

3. Trial Design

The registry identifies this as a randomized, parallel-group trial with no masking. Participants were assigned to oral nifedipine or oral labetalol. The recorded enrollment is 50, and the posted outcome results include 25 participants in each arm. The trial is marked completed. The registry lists the phase as NA, which does not provide a phase classification.

The arms are described as nifedipine XL starting at 30mg orally once daily and labetalol starting at 200mg orally twice daily. Those descriptions identify starting doses, but the registry does not report whether doses could be adjusted, which additional treatments were permitted, or how treatment was managed if the blood pressure goal was not attained. Further protocol details are not reported in the registry record.

The primary endpoint is mean time in hours to attain sustained blood pressure goal after antihypertensive medication was initiated. Its stated timeframe is 24 hours. The record also reports total length of hospital stay in days as a secondary outcome, with a stated timeframe of 0-10 days. Although the study summary mentions shortening hospital stay as an aim, the registry labels hospital stay as secondary rather than primary.

The record lists a start date of 2014-06 and a primary completion date of 2015-06. These registry dates do not by themselves explain when outcomes were assessed for each participant or whether all participants completed follow-up. Participant flow, withdrawals, protocol deviations, and the analysis population for each outcome are not reported in the registry record.

Randomization can reduce systematic differences between assigned groups, but the registry does not describe the random sequence generation or allocation concealment. With no masking, participants and study personnel were not masked according to the recorded design. The record does not describe whether outcome assessors were masked. These details matter when interpreting outcomes that involve clinical decisions or judgments, including the determination that a sustained blood pressure goal has been attained.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Time (Hours) to Attain Sustained Blood Pressure Goal After Treatment Initiated With Antihypertensive Medication, measured over 24 hours.

The primary endpoint measures elapsed time, in hours, from initiation of antihypertensive medication until a sustained blood pressure goal is attained. It is a continuous outcome: each participant’s time can take a range of values, and the posted results summarize the groups using means and standard deviations. The registry gives 24 hours as the endpoint timeframe.

Time to goal is relevant to the stated study question because the study aimed to compare how quickly the two oral medications were associated with reaching the target. A time measure can capture differences that a simple yes-or-no measure at a single assessment might not show. The word “sustained” indicates that the endpoint concerns more than an isolated reading, but the registry does not define the required duration or number of readings. The blood pressure threshold itself is also not reported in the registry record.

The posted group means are 37.6 hours for labetalol and 38.2 hours for nifedipine. Their standard deviations are 32.5 and 27.6 hours, respectively. The comparison is a mean difference of 0.6 hours for nifedipine relative to labetalol. These are group-level summaries; they do not show the distribution of individual times, how many participants attained the goal within a particular interval, or how participants who did not attain it were handled.

The endpoint is therefore interpretable only within the operational definitions and follow-up procedures used in the trial. Those details are not reported in the registry record, so the posted means should not be taken as a complete description of the clinical process or each participant’s course.

7. Results Posted in the Registry

• Nifedipine: mean 38.20 versus 37.60 on control; difference 0.60 (95% CI -16.11 to 17.31), standardized effect d = 0.02; z-test p = 0.944.

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.

Total Length of Hospital Stay in Days

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Nifedipine: mean 4.30 versus 4.00 on control; difference 0.30 (95% CI -0.78 to 1.38), standardized effect d = 0.15; z-test p = 0.585.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nifedipine and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint: total length of hospital stay in days. Its group summaries show means and standard deviations, and the posted comparison is a mean difference with a confidence interval and unadjusted p-value. The interval includes zero, so the secondary result is also compatible with no mean difference as well as with differences in either direction.

Across the primary and secondary outcomes, the posted results do not provide a precise separation between the arms. The secondary comparison does not supply a clear corroborating signal that resolves the uncertainty in the primary time-to-goal result. It is best read as an additional descriptive comparison, not as independent confirmation of a treatment effect or of equivalence.

The study summary mentions shortening hospital stay among its aims, but the registry labels total hospital stay as a secondary outcome. That distinction matters when weighing the evidence: the primary question concerns time to sustained blood pressure goal, while length of stay is an additional outcome. The record does not explain whether the hospital-stay analysis was prespecified, whether it was intended to support a formal claim, or how it was prioritized relative to the primary endpoint.

Unadjusted secondary results carry less weight when multiple outcomes may be examined because the chance of observing an apparently notable result can increase across a set of comparisons. General: multiplicity methods can control or otherwise address that issue, but the appropriate approach depends on the study’s planned questions and analysis strategy. The registry does not report a multiplicity adjustment or an analysis plan, so no adjustment should be assumed. The secondary result should not be treated as a confirmatory finding on its own.

The number of outcome measures and analyses listed in the record does not establish how many comparisons were planned or considered by investigators. The registry reports one posted secondary endpoint and zero reported analyses, but further details are not reported in the registry record. Interpretation is consequently limited to the posted descriptive summaries and unadjusted comparison.

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

• Total Length of Hospital Stay in Days

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a continuous primary outcome summarized by a mean and standard deviation for each arm. For labetalol, the reported mean time to sustained blood pressure goal is 37.6 hours with a standard deviation of 32.5 hours; for nifedipine, the mean is 38.2 hours with a standard deviation of 27.6 hours. A mean describes the arithmetic average across the participants included in the summary. A standard deviation describes how spread out individual observations are around that mean. It is not the uncertainty in the mean itself.

What does the mean difference represent?

The posted contrast is the nifedipine mean minus the labetalol mean. It is reported as 0.6 hours. A value of zero would represent equal group means; a positive value indicates a higher observed mean in the nifedipine arm, and a negative value would indicate a lower observed mean in that arm. The contrast concerns group averages, not a statement that every participant had a time close to the group mean. The registry does not report the individual participant data or a distributional plot of individual times.

How should the confidence interval be read?

General: a confidence interval expresses the uncertainty of an estimate under the statistical method used. A narrower interval indicates greater precision, while a wider interval indicates less precision. For the primary mean difference, the posted interval runs from -16.11 to 17.31 hours. Because it includes zero and values on both sides of zero, the data do not pin down the direction of the mean difference with precision. The registry record does not describe the method used to construct this interval, so the calculation method should not be inferred.

What does the p-value say?

The posted unadjusted p-value for the primary comparison is 0.944. General: a p-value measures how incompatible the observed data are with a specified null model, conditional on the assumptions of the test. It is not the probability that the null hypothesis is true, nor is it the probability that the result occurred “by chance.” A large p-value is not proof of no difference. The record calls this result unadjusted and does not report a formal analysis plan or other details about the test used.

General: a p-value also does not measure the size or clinical importance of an effect. The mean difference and its interval are needed to understand the estimate and its precision. For that reason, the primary result should be read from the point estimate together with the interval, rather than treating the p-value as a stand-alone verdict. The registry does not report a threshold for a clinically important difference in time to goal.

Why does variability matter?

General: when observations vary substantially within groups, it can be harder to estimate a difference between group means precisely, especially when the groups are small. The standard deviations for the primary outcome are large relative to the reported difference, and the confidence interval is correspondingly broad. This explains why an observed difference near zero can coexist with uncertainty about appreciably lower or higher mean times. It does not establish that the groups are identical.

General: over-dispersion refers to more variability in data than a statistical model assumes. It can make model-based standard errors too small if the extra variability is ignored. The posted primary endpoint is reported as a continuous mean and standard deviation, and the record does not report an over-dispersion assessment or a model that would allow such an assessment. It would therefore be inappropriate to claim that over-dispersion was tested or corrected.

What is and is not reported about the analysis?

The registry lists zero reported analyses. It nevertheless posts arm-level outcome summaries and comparison statistics. It does not describe the statistical test, covariate adjustment, handling of missing observations, the analysis population, or whether any sensitivity analyses were conducted. These are not reported in the registry record. The posted comparison should therefore be described as an unadjusted mean comparison rather than attributed to an undocumented model.

General: random assignment supports a comparison of groups as assigned, but the interpretation still depends on the analysis population, follow-up, missing data, and implementation of randomization. The registry identifies randomized allocation but does not report sequence generation, concealment, participant flow, or an intention-to-treat analysis. Those omissions limit the ability to assess the full analysis process from the registry record alone.

What do planning calculations mean?

The sample-size planning values are illustrations based on the observed effect, not documentation of the trial’s original design. General: a power calculation estimates how many participants a hypothetical study might require to detect a specified effect under stated assumptions. Power is the probability of detecting that effect according to those assumptions if the effect is present. A smaller target effect generally requires more participants to distinguish it from random variation, all else being equal. Such a calculation does not tell how likely the posted result was to be significant after the trial was completed.

The registry does not report an original sample-size justification or the assumptions used when the trial was planned. It also does not report interim analyses, stopping rules, a prespecified statistical analysis plan, or adjustments for multiple comparisons. None of these procedures should be assumed from the posted summary statistics.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the group difference. For the primary endpoint, the posted mean difference is 0.6 hours, with a confidence interval from -16.11 to 17.31 hours. That interval includes zero and spans values favoring either direction. It therefore indicates substantial uncertainty about the size and direction of the mean difference, rather than a tightly estimated effect.

A confidence interval is not a range containing a fixed proportion of individual participants’ times. It describes uncertainty about the estimated contrast under the method used to calculate it. The registry does not report the interval construction method. Its width should be read alongside the small group sizes and the standard deviations reported for the endpoint, rather than as a direct description of individual outcomes.

The interval is compatible with no mean difference, but it is also compatible with differences that may be important to the study question. The registry does not state what size of difference would be clinically important, so the confidence interval cannot be judged against a prespecified clinical threshold. Without such a threshold, the result supports a conclusion about statistical uncertainty, not a categorical conclusion about equivalence or practical importance.

The unadjusted p-value of 0.944 does not resolve this imprecision. It indicates that the posted unadjusted comparison does not provide evidence against a no-difference null model, but it does not show that no difference exists. A broad interval and a non-significant result are consistent with limited information in the observed sample. They should not be described as proof that the two arms have identical outcomes.

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, not total event counts. The primary endpoint and the secondary hospital-stay endpoint are continuous outcomes, so the planning display gives participants per arm. The event-count convention for time-to-event outcomes does not apply to these reported outcomes.

The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its reference and considers planning for 100%, 75%, and 50% of that observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record. The planning values are therefore hypothetical illustrations, not a description of how the trial’s enrollment target was chosen.

The 80% power column gives the participants per arm estimated to provide an 80% chance of detecting the specified effect under those assumptions, if that effect is present. The 90% power column gives the corresponding estimate for a higher chance of detection. Neither column is the number enrolled in the completed trial; the posted outcome groups each contain 25 participants.

As the target effect becomes smaller, the estimated number of participants per arm increases. A smaller difference is harder to distinguish from random variation under otherwise unchanged assumptions. These values are planning illustrations, not observed power. They do not measure the probability that the trial’s findings are true or the probability that a result will be statistically significant after the fact.

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 = 0.600; pooled standard deviation σ = 30.150.
2. n = 2 × (1.96 + 0.842)² × 30.150² / 0.600² = 39,637.1, rounded up to 39,638 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.600000000000001                      # observed difference in means
sigma <- 30.1497097830145                     # 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(2168309)
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 = 39,638 (80% power), 53,063 (90% power)
 75% of observed effect: n per arm = 70,466 (80% power), 94,334 (90% power)
 50% of observed effect: n per arm = 158,549 (80% power), 212,252 (90% power)
power.t.test: 39638 
Simulated power at n = 39,638 per arm: 0.800 (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 identifies a primary endpoint and one secondary endpoint, but it does not report a statistical analysis plan describing how the outcomes were prioritized or analyzed. It lists zero reported analyses. The posted outcome comparisons include unadjusted p-values, and no correction for multiple comparisons is reported in the registry record.

Multiplicity arises when several hypotheses or outcomes are tested. General: considering more comparisons can increase the chance that at least one result appears notable even when the underlying effects are absent. Researchers may address multiplicity through a prespecified hierarchy, adjusted significance thresholds, or other methods. Which approach is appropriate depends on the trial’s objectives. No such strategy is reported, so the secondary result should be interpreted cautiously and not treated as a confirmatory test.

The record does not report an analysis population for either endpoint. It does not state whether analyses included all randomized participants, only participants with observed outcomes, or another defined group. It also does not describe participant flow, missing outcome counts, reasons for missingness, or methods for handling missing data. Imputation, complete-case analysis, and sensitivity analyses are not reported in the registry record.

Randomized allocation is recorded, but details of sequence generation and allocation concealment are not reported. Masking is recorded as none; whether outcome assessors were masked is not reported. These details can inform assessment of possible bias, especially for an endpoint whose measurement may depend on the timing and confirmation of blood pressure readings.

The registry does not report interim analyses, stopping rules, protocol deviations, adjustments for baseline characteristics, or a prespecified threshold for a clinically important difference. Their absence from the record does not establish that they were or were not used; these items are not reported in the registry record. The results can therefore be interpreted from the posted estimates, while the design and analysis safeguards remain incompletely documented.

15. 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.

For both arms, the registry lists 25 participants at risk for serious adverse events and 0 affected. It also lists 25 participants at risk for other adverse events and 0 affected in each arm. No serious adverse-event terms are listed among the top terms.

These entries mean that the posted record reports zero participants affected in the recorded categories. They do not establish that the risk of an adverse event is absent. The sample is limited, and the registry does not provide event-level descriptions or further detail about how events were collected, classified, or monitored. Death counts are null for both arms, so deaths are not reported in the registry record; null is not the same as a reported count of zero.

Safety figures should be interpreted as registry reporting for the recorded categories and at-risk groups, not as a complete account of every possible adverse experience. The record does not report further safety analyses or comparisons. These figures alone do not support conclusions about the relative safety of the medications.

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

The posted results describe a randomized comparison of two oral medications in a trial enrolling 50 participants. For the primary outcome, the observed group means are close, but the estimate is imprecise: the confidence interval includes no mean difference and allows differences in either direction. The unadjusted p-value does not provide evidence against a no-difference comparison. Together, these results do not establish the stated superiority hypothesis.

They also do not establish that the treatments are equivalent. A non-significant comparison can arise when the data are too limited to distinguish a difference from no difference. An equivalence conclusion would require an agreed margin for differences that count as practically equivalent, along with a suitable design and analysis. The registry does not report such a margin or an equivalence objective.

The posted means are group summaries, not guarantees about individual outcomes. They do not reveal how many participants reached the goal quickly, how individual experiences varied, or how missed measurements were handled. The registry does not define the blood pressure goal, the duration required for it to count as sustained, or the analysis population. Those omissions constrain the clinical interpretation of the endpoint.

The secondary hospital-stay comparison also does not resolve the uncertainty in the primary result. It is an unadjusted secondary finding, and no multiplicity strategy is reported. The safety entries report no participants affected in the listed serious or other adverse-event categories, but those entries do not establish absence of risk, and death counts are not reported.

Overall, the record supports a cautious statistical reading: the observed estimates do not show a clear separation between the arms, and the primary estimate is too imprecise to rule out a range of possible differences. This is a statement about the posted data and their limits, not medical advice and not a conclusion that either medication should or should not be used.

17. Why This Trial Matters Statistically

This trial illustrates why an estimate, its uncertainty, and the study’s design details all matter together. The primary mean difference is near zero, but the confidence interval is wide enough to include possible effects in either direction. A reader who focused only on the p-value might mistake a result that does not reach statistical significance for evidence of no difference. The interval shows why that interpretation would be too strong.

The study also makes the distinction between a stated hypothesis and evidence from the posted results visible. The registry summary describes a superiority hypothesis, but the observed comparison does not establish superiority. Assessing the hypothesis requires attention to the direction and size of the estimate, its precision, and the analysis plan—not only to the study’s stated aim.

The enrollment and outcome variability are important context. With 25 participants in each posted group and considerable spread in the primary measure, the result leaves substantial uncertainty. The planning illustrations make a related general point: detecting smaller effects generally requires larger samples under otherwise similar assumptions. Those illustrations do not explain the original enrollment decision, which is not reported.

Finally, the record distinguishes the primary question from the secondary hospital-stay outcome, but does not document a multiplicity strategy, analysis populations, missing-data methods, or a statistical analysis plan. That lack of documentation limits how strongly the secondary result can be interpreted and how fully the analysis can be audited. Clear reporting of estimands, outcome definitions, participant flow, and analysis choices is essential for turning summary results into a well-supported interpretation.

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 limitations are specific to the information recorded for this trial. The total enrollment is 50, with 25 participants in each posted arm. The primary outcome has substantial within-group variation relative to the observed mean difference, and its confidence interval is wide. As a result, the data provide limited precision for distinguishing the arms.

The trial is recorded as open-label. Masking was none, and the registry does not report whether outcome assessors were masked. The primary endpoint depends on when a sustained blood pressure goal is judged to have been attained. The numerical goal, required duration of control, measurement schedule, and rules for confirming attainment are not reported in the registry record.

The posted summaries do not disclose participant flow, outcome completeness, missing-data handling, or analysis populations. It is therefore not possible from the registry record to establish whether all randomized participants contributed to each result or to assess potential effects of missing observations. Details of random sequence generation and allocation concealment are also not reported.

The registry does not report dose-adjustment rules, permitted additional therapies, protocol deviations, or the original sample-size justification. It also lists zero reported analyses and does not provide a statistical analysis plan, multiplicity method, or clinically important difference threshold. The secondary endpoint is unadjusted, and the record does not state how it was intended to contribute to the study’s conclusions.

Safety reporting is limited to the counts recorded for serious and other adverse events; event descriptions and further safety analyses are not reported. Death counts are not reported in the registry record. These gaps do not demonstrate that procedures or events were absent, but they limit what can be concluded from the registry information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Oral Nifedipine Versus Oral Labetalol — NCT02168309.
• Registry record last updated 2017-12-13; status last verified 2017-11.
• Results first posted 2017-12-13.
• 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 record identifies NCT02168309 as “Oral Nifedipine Versus Oral Labetalol,” sponsored by Cedars-Sinai Medical Center. It describes a randomized, open-label, parallel-group trial for severe postpartum hypertension and lists the status as completed. The recorded enrollment is 50.

The primary outcome is time in hours to attain sustained blood pressure goal after antihypertensive medication is initiated, with a stated timeframe of 24 hours. The posted results include 25 participants per arm and an unadjusted mean comparison. Total length of hospital stay in days is listed as a secondary outcome.

The record lists a start date of 2014-06 and a primary completion date of 2015-06. The phase is listed as NA. Further details about the analysis plan, missing data, participant flow, and outcome definitions are not reported in the registry record.