Comparing Nifedipine and Enalapril in Medical Resources Used in the Postpartum Period: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing Nifedipine and Enalapril in Medical Resources Used in the Postpartum Period (NCT04236258), a randomized phase 4 study. The primary outcome is Prolonged Hospitalization.

2. Clinical Question

The registry describes the broader aim as comparing medical resources used after delivery. Its primary outcome focuses more narrowly on prolonged hospitalization. Other listed outcomes address blood-pressure control, additional antihypertensive treatment, discharge timing, blood-pressure events, creatinine, continued treatment, side effects, and self-reported adherence. These measures give context about care and treatment during the postpartum period, but they are not interchangeable with the primary outcome.

The randomized comparison can address differences between the assigned starting treatments within the trial population. It does not, by itself, resolve questions about other treatment regimens, populations not represented in the record, or outcomes beyond the reported follow-up period. The registry record does not report detailed eligibility criteria or a fuller description of the population beyond the arm descriptions and listed conditions.

3. Trial Design

This was a randomized, parallel-group phase 4 trial with no masking. The registry reports enrollment of 94 and lists 47 participants in each arm for the primary outcome. One group was assigned to start nifedipine extended release 30 mg daily; the other was assigned to start enalapril 10 mg daily. The trial is marked completed. Its recorded start date is 2020-01-24, and its primary completion date is 2021-06-30.

Random allocation is intended to make treatment groups comparable, on average, with respect to characteristics that could affect outcomes. In a parallel design, participants are assigned to one treatment group rather than receiving both treatments in sequence. The registry does not report details of how the random sequence was generated, whether assignment was concealed before treatment allocation, or whether any stratification was used. The lack of masking means the study is recorded as open-label; further details about who knew assignments are not reported in the registry record.

The primary endpoint was the number of participants with any postpartum hospitalization extending beyond the normal length of stay after delivery, assessed up to six weeks postpartum. The registry also lists secondary outcomes, including time to blood-pressure control and time to discharge. The posted summaries include results for several secondary outcomes, but a detailed statistical analysis plan and a complete account of outcome-specific analysis populations are not reported in the registry record.

The brief summary contains an inconsistency: it says that half of participants would receive enalapril while the other half would also receive enalapril. The arm descriptions and posted results instead identify nifedipine and enalapril as the two groups. This discrepancy is relevant when interpreting the narrative description, even though the listed arms clearly distinguish the treatments. The original design assumptions, including any original sample-size justification, 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.

Before assignment: We aimed for 90 participants as part of the protocol but ended up oversampling at 94 due to concern over potential drop out.

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 Prolonged Hospitalization, measured over up to six weeks postpartum.

The primary endpoint counts participants who had any postpartum hospitalization that extended beyond the normal length of stay after delivery. The assessment timeframe was up to six weeks postpartum. The measure is a participant count: each participant is classified according to whether the specified prolonged-hospitalization event occurred. It is not a count of hospital days or a combined measure of all medical resources.

This outcome is relevant to the trial’s stated interest in postpartum medical-resource use because a hospitalization beyond the usual stay represents continued inpatient care. It offers a clear event-based way to compare the two assigned treatment groups. The registry’s broader summary also mentions unscheduled medical visits and hospital readmissions as resource-use outcomes, but those are not part of the posted primary endpoint definition. The primary outcome should therefore be interpreted according to its specific definition rather than as a comprehensive measure of all resource use.

For the primary result, the registry reports 13 participants in the nifedipine arm and 17 in the enalapril arm, with 47 in each arm. The comparison is expressed as a risk difference for enalapril relative to nifedipine. A positive difference indicates a higher observed event proportion in the enalapril group, while the confidence interval describes uncertainty around the estimated difference. The interval includes both negative and positive values, so the estimate is not precise enough to establish the direction of the underlying difference.

7. Results Posted in the Registry

• Enalapril: 36.2% (17/47) versus 27.7% (13/47) on control; risk difference 8.5 percentage points (95% CI -10.3 to 27.3), risk ratio 1.31 (0.72–2.38); unadjusted two-proportion z-test p = 0.376.

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.

Time to Blood Pressure Control

• 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:
  • Enalapril: mean 1.90 versus 0.70 on control; difference 1.20 (95% CI 0.16 to 2.24), standardized effect d = 0.47; z-test p = 0.024.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Enalapril than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Who Needed for Additional Antihypertensives

• 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:
  • Enalapril: 34.0% (16/47) versus 12.8% (6/47) on control; risk difference 21.3 percentage points (95% CI 4.7 to 37.8), risk ratio 2.67 (1.14–6.22); unadjusted two-proportion z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Enalapril than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time to Discharge

• 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:
  • Enalapril: mean 3.30 versus 3.20 on control; difference 0.10 (95% CI -0.57 to 0.77), standardized effect d = 0.06; z-test p = 0.769.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enalapril and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the picture beyond prolonged hospitalization. They cover the speed of blood-pressure control, whether additional antihypertensive treatment was needed, time to discharge, clinically significant blood-pressure events, creatinine after discharge, continued need for treatment, side effects, and self-reported adherence. Together, these measures concern treatment course and postpartum care, but they do not measure the primary endpoint directly.

The posted summaries show a mixed pattern rather than a single consistent signal across all these domains. Some comparisons point toward differences between the groups, while another is close to no estimated difference; uncertainty also varies by outcome. This pattern does not establish that the secondary measures explain the primary result. For example, needing additional medication and experiencing a prolonged hospitalization are distinct outcomes, even when both may be relevant to postpartum care.

Secondary results can help generate questions for further study, but they carry less weight than a prespecified primary analysis when their interpretation is unadjusted. Examining multiple outcomes makes it more likely that at least one result will appear notable by chance. The registry record does not report a multiplicity strategy, a formal hierarchy for secondary outcomes, or reported analyses beyond the posted summaries. The secondary p-values therefore should not be treated as independently confirmatory evidence.

Some listed secondary outcomes do not have detailed results in the posted record. Their absence from the displayed result summaries does not establish that the outcomes were not measured or that no events occurred. Outcome-specific results, analysis populations, missingness, and analytic methods are not reported in the registry record where not otherwise stated. These limits make it difficult to assess how complete the overall secondary-outcome picture is.

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

• Time to Blood Pressure Control
• Number of Participants Who Needed for Additional Antihypertensives
• Time to Discharge
• Clinically Significant Hypotension or Hypertension
• Creatinine Values at 1-2 Weeks After Discharge
• Continued Need for Antihypertensive
• Number of Participants With Self-reported Side Effects Attributed to the Antihypertensive They Received
• Patient Self-reported Compliance With Their Antihypertensive Regimen

9. Statistical Interpretation

10. Statistical Methods Explained

Randomization assigns participants to treatment groups by chance. In general, this helps reduce systematic differences between groups at the point of assignment, although chance imbalances remain possible, especially in a study with limited enrollment. A parallel-group trial follows the assigned groups separately rather than comparing each participant under both treatments. This trial is recorded as randomized and parallel, with no masking. The specific randomization procedure and allocation-concealment methods are not reported in the registry record.

How to read the event comparison

The primary endpoint is binary at the participant level: a participant either had a prolonged postpartum hospitalization as defined or did not. The arm results report event counts and the number assessed in each arm. The risk difference expresses the difference between the event proportions in the two groups, here with enalapril compared with nifedipine. A positive risk difference means the observed proportion is higher in the enalapril arm; a negative value means it is higher in the nifedipine arm. This direction describes the comparison and is not, by itself, a judgment about clinical importance.

A confidence interval gives a range of values compatible with the observed data under the statistical method used. Its width reflects uncertainty: a wider interval indicates less precision. When an interval for a risk difference crosses zero, the data are compatible with no difference as well as with differences in either direction. The interval does not assign equal probability to every value within its limits, and it does not represent the range of outcomes for individual participants.

An unadjusted p-value measures how incompatible 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, nor does it measure the size or clinical importance of a difference. The registry reports unadjusted p-values for the posted comparisons. It does not report the test specifications, a prespecified significance threshold for the trial’s own analyses, or any adjustment for multiple comparisons. The 0.05 level mentioned for planning illustrations is an assumption for those illustrations, not a reported trial analysis threshold.

How to read mean comparisons

For continuous outcomes, the registry reports arm means and standard deviations, followed by a mean difference. The mean difference is the average outcome in the enalapril group minus the average in the nifedipine group. A positive value therefore indicates a higher mean in the enalapril group on the outcome’s stated scale. Standard deviation describes variation among observations within an arm; it is not the uncertainty around the mean difference. The confidence interval for the mean difference is the more direct summary of uncertainty in that comparison.

For time to blood-pressure control and time to discharge, the outcome unit is days. Those outcomes are reported as means, not as time-to-event estimates with censoring information. The registry record does not report whether all participants had complete follow-up for these measures, how any incomplete observations were handled, or whether any model accounted for the timing or censoring of events. The posted summaries should therefore be read as the stated means and unadjusted comparisons, without assuming a particular unreported model.

Why analysis details matter

An analysis plan ordinarily specifies the primary analysis population, handling of missing values, comparison method, and treatment of multiple outcomes before results are examined. These details help readers judge whether the reported analysis followed the intended plan and how much weight to give secondary findings. The registry lists no reported analyses, and a detailed plan covering these choices is not reported in the registry record. It is not possible to determine from the posted summaries whether the analyses followed an intention-to-treat, per-protocol, or other population definition.

Multiplicity arises when investigators test or estimate effects for more than one outcome or comparison. Even if each test is conducted using a fixed error rate, a collection of tests can produce a seemingly notable result by chance. Adjusting for multiplicity can limit this issue, but adjustments also affect interpretation and precision. No adjustment is reported for the secondary comparisons. Their p-values should consequently be viewed as unadjusted evidence rather than as confirmatory results with a reported family-wise error control.

Planning calculations are not trial power

The sample-size illustrations use the observed effect as a reference and consider detecting a stated fraction of that effect. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The trial’s original design assumptions and original sample-size justification are not reported in the registry record. These planning calculations are distinct from the trial design and do not show the probability that the completed trial detected an effect.

In general, over-dispersion matters when count outcomes vary more than a model assumes; ignoring it can make uncertainty estimates too small. That issue is a general statistical consideration, not a reported feature of this trial’s primary outcome analysis. The primary measure is a participant event count in each arm, and no model-based adjustment for over-dispersion is reported. Similarly, a general statistical explanation should not be mistaken for evidence that a particular method was used in the trial.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of 0.085 for enalapril compared with nifedipine. Its 95% confidence interval extends from -0.103 to 0.273. Because the interval crosses zero, the posted data are compatible with a lower event proportion in the enalapril group, no difference, or a higher event proportion. Its span indicates considerable uncertainty about the size of the difference. The point estimate is only one value within that uncertainty range.

Precision depends on the amount of information available and on variation in the data, among other factors. The primary outcome has 47 participants in each arm, and the posted event counts are 13 and 17. These registry entries describe the available comparison; they do not establish whether the trial met a particular precision target, because the original target and its assumptions are not reported in the registry record.

A confidence interval is not a guarantee that the true effect lies within its limits, and it is not a range containing most individual outcomes. In repeated use of the same method under its assumptions, intervals constructed in this way would cover the underlying parameter at the stated rate. For a reader assessing this result, the practical point is that the interval does not pin down the direction of the difference. A p-value of 0.376 is consistent with that uncertainty, but it cannot substitute for examining the interval and estimate.

The secondary comparisons also vary in precision. Their intervals are wider or narrower according to their estimates and data, and some include values compatible with no difference. The registry record does not report adjusted confidence intervals accounting for multiple outcomes. Precision should therefore be judged outcome by outcome, with attention to the interval as well as the point estimate, and with recognition that unadjusted secondary estimates have additional interpretive uncertainty.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design target. For the non-time-to-event outcomes, the figures refer to participants per arm. A time-to-event planning display, if used, instead gives the total number of events; the stated sample-size assumptions distinguish that convention from participant counts per arm. The planning calculations assume two-sided significance at 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

Read each planning scenario by first identifying the fraction of the observed effect used, then the desired power level. The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of rejecting the null hypothesis under the specified assumptions if the assumed effect were true. The 90% column gives the corresponding number for a higher probability of detecting that assumed effect. Neither column says how likely the completed trial was to find an effect, and these figures are not observed power.

The illustrations also show why the assumed effect matters. Planning for 75% of the observed effect or 50% of the observed effect requires more participants per arm than planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so more information is generally needed to detect them at the same power and significance level. The observed effect is itself uncertain, particularly in a trial with limited enrollment, so using it as the planning reference should not be treated as a reliable forecast of the effect in a future study.

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 = 0.277; treatment proportion p₁ = 0.362; average p̄ = 0.319.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6592 = 1.2921.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6565 = 0.5525.
4. n = (1.2921 + 0.5525)² / (0.0851)² = 469.8, rounded up to 470 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 <- 0.276595744680851                          # control proportion
p1 <- 0.361702127659574                          # 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(4236258)
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 = 470 (80% power), 629 (90% power)
 75% of observed effect: n per arm = 821 (80% power), 1,099 (90% power)
 50% of observed effect: n per arm = 1,812 (80% power), 2,426 (90% power)
power.prop.test: 469.8 
Simulated power at n = 470 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes. When several hypotheses are examined, the chance of at least one result appearing notable by chance can rise. This is the multiplicity problem. Common approaches include adjusting the significance threshold, using a prespecified testing sequence, or labeling secondary analyses as exploratory. The registry record does not report which approach, if any, was planned or used.

The posted secondary comparisons include unadjusted p-values. Without a reported multiplicity strategy, these values should be interpreted as individual, unadjusted comparisons rather than as a set with controlled overall error. The record does not specify which secondary outcomes were prioritized, whether a hierarchy was prespecified, or whether all planned comparisons are posted. It is therefore not possible to assess the full multiplicity burden from the registry record alone.

Missing-data methods and analysis populations are also important. A reader needs to know whether participants were analyzed according to original assignment, whether any participants were excluded from specific outcomes, and how missing measurements were handled. The registry lists arm-level denominators for the posted outcomes, but does not report a complete account of missing observations, exclusions, or analysis-population definitions. Intention-to-treat, per-protocol, and other analysis populations should not be inferred from the arm counts alone.

The statistical analysis plan, including its timing relative to outcome review, is not reported in the registry record. Interim analyses and any stopping rules are also not reported in the registry record. These absences do not show that such plans or procedures were absent in practice; they mean that their presence and details cannot be assessed from the record. This limits evaluation of whether the posted analyses were prespecified and how outcome selection or repeated testing may have affected interpretation.

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 zero serious adverse events in the nifedipine group and zero in the enalapril group. It also reports zero other adverse events in both groups and zero deaths in both groups. The adverse-event figures list 47 participants at risk in each arm for serious and other adverse events.

These are the reported counts in the registry record. They describe what is posted for this trial; they do not establish that a treatment has no safety risks. The record does not provide serious adverse-event terms, and the list of top serious terms is empty. It also does not describe in detail how adverse events were solicited, classified, or attributed. The separate secondary outcome concerning self-reported side effects should not be conflated with the serious and other adverse-event counts. The registry record does not report enough detail to reconcile those measures or to infer why their reporting differs.

Zero recorded events in a trial of this size still leave uncertainty about uncommon outcomes. Safety conclusions require attention to the event definitions, observation period, completeness of reporting, and the amount of information available. These details should be assessed from the registry record and any fuller trial report, rather than inferred from zero counts alone.

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

The primary result is an estimate of the difference in prolonged-hospitalization event proportions between the two randomized groups over the stated postpartum timeframe. The observed estimate favors neither a firm conclusion about direction nor a precise estimate of size: its confidence interval includes zero and values on both sides. The posted p-value likewise does not provide evidence of a clear difference under the unadjusted comparison. These results describe uncertainty; they do not prove equivalence or absence of an effect.

The result is limited to the defined endpoint and the participants represented in this trial. It does not directly answer whether the treatments differ for every resource-use outcome mentioned in the trial summary, since the primary endpoint is prolonged hospitalization rather than a combined measure of visits, readmissions, and inpatient duration. Nor does it establish what would happen beyond the stated follow-up period or in populations not described by the registry record.

Randomization is a useful design feature for comparing assigned groups, but it does not remove uncertainty from limited data, guarantee balance on every characteristic, or resolve missing analysis details. The record does not report the original sample-size justification, a full analysis plan, outcome-specific missing-data handling, or multiplicity procedures. Those omissions restrict how confidently the posted estimates can be placed in a broader confirmatory framework.

Secondary outcomes provide additional descriptive information about postpartum care and treatment, but their unadjusted status and the absence of a reported multiplicity plan mean that isolated findings deserve caution. They may inform questions for future research, but should not be elevated above the primary comparison or treated as definitive evidence on their own. No treatment recommendation follows from the registry results alone.

The brief summary’s assignment inconsistency is another reason to distinguish the narrative from the arm-level record. The arm descriptions and posted results name nifedipine and enalapril, while one sentence in the summary names enalapril for both groups. The record does not report a correction or clarification of that sentence. Readers should recognize the inconsistency when interpreting the study description.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through both its estimate and its uncertainty. The primary point estimate is not enough to establish a difference, and a nonsignificant unadjusted p-value is not evidence that treatments are equivalent. The confidence interval communicates that the result remains compatible with effects in either direction. This distinction is central to responsible interpretation of clinical trial results.

It also highlights the importance of matching the endpoint to the broader research question. The stated interest is medical-resource use in the postpartum period, while the primary endpoint measures prolonged hospitalization. Other listed outcomes address separate aspects of care. Clear definitions help prevent a narrow endpoint from being interpreted as a complete measure of resource use or overall clinical experience.

The secondary outcomes demonstrate why multiplicity and prespecification matter. A set of unadjusted comparisons may produce estimates that look more compelling in isolation than they do as part of a broader outcome family. Without a reported testing hierarchy or multiplicity adjustment, the results are best read as a set of descriptive and potentially hypothesis-generating findings, not as a collection of independent confirmations.

Finally, the registry record shows the value of complete reporting. Details about the original design assumptions, analysis populations, missing data, and analysis plan would help readers assess precision and the strength of inference. The inconsistency in the brief treatment-assignment sentence also shows why narrative descriptions should be checked against arm-level information. Transparent reporting supports interpretation without requiring readers to fill gaps by assumption.

18. Limitations

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

The posted primary comparison has limited precision: its confidence interval includes zero and extends across both negative and positive differences. The record does not report the original sample-size justification or target effect, so it is not possible to determine whether the trial was designed to estimate the primary outcome with a particular level of precision. The planning illustrations based on observed effects do not replace those missing design details.

The registry records no masking. Knowledge of assignment could matter for outcomes involving clinical decisions, participant reports, or discharge processes, although the record does not establish that it affected any result. Details about allocation concealment and the randomization procedure are also not reported. The treatment-assignment sentence in the brief summary is inconsistent with the two arm descriptions and adds uncertainty to the narrative account.

The record does not report detailed methods for missing data, analysis populations, multiplicity, interim analyses, or the trial’s statistical analysis plan. It also does not provide a full account of adverse-event ascertainment or serious-event terms. These reporting gaps limit appraisal of analytic choices and completeness. They should not be mistaken for proof that a method or procedure was not used.

The primary endpoint captures prolonged hospitalization as defined, not all forms of medical-resource use mentioned in the summary. Follow-up is described as up to six weeks postpartum, and conclusions should remain within that time horizon. The registry’s listed conditions and arm descriptions do not provide a full account of eligibility criteria or participant characteristics, limiting assessment of how closely the trial population matches other clinical settings.

Finally, the secondary findings are unadjusted in the posted record, and no multiplicity approach is reported. They may be useful for context but require cautious interpretation. The record does not report enough information to evaluate whether every planned outcome or analysis is represented in the posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparing Nifedipine and Enalapril in Medical Resources Used in the Postpartum Period — NCT04236258.
• Registry record last updated 2022-11-30; status last verified 2022-11.
• Results first posted 2022-11-30.
• 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

NCT04236258 is a completed randomized, parallel-group phase 4 trial sponsored by Brigham and Women's Hospital. It compared starting nifedipine extended release 30 mg daily with starting enalapril 10 mg daily among postpartum women needing antihypertensive treatment. The registry reports enrollment of 94 and a primary completion date of 2021-06-30.

The primary outcome was participants with a postpartum hospitalization extending beyond the normal length of stay after delivery, assessed up to six weeks postpartum. The posted comparison showed an estimated risk difference of 0.085 for enalapril versus nifedipine, with a 95% confidence interval from -0.103 to 0.273 and an unadjusted p-value of 0.376. The interval includes zero and leaves the direction and size of the difference uncertain.

Secondary outcomes and adverse-event counts provide additional context, but their interpretation is limited by unadjusted comparisons and reporting details that are not reported in the registry record. The brief summary also contains an inconsistent sentence about the assigned treatments; the arm descriptions and posted results identify nifedipine and enalapril.