Programmed Intermittent Epidural Bolus Versus Continuous Epidural Infusion for Termination of Pregnancy Analgesia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Programmed Intermittent Epidural Bolus Versus Continuous Epidural Infusion for Termination of Pregnancy Analgesia (NCT01860521), a randomized na study. The primary outcome is Incidence of Motor Block.

2. Clinical Question

The study also recorded patient satisfaction at hospital discharge and total levobupivacaine and sufentanil consumption. These outcomes address different aspects of the analgesia experience and its use; they are secondary to the motor-block endpoint in the registry listing. The registry describes the study as randomized and parallel-group. Its masking entry is quadruple, while the brief summary calls it double-blind; the record does not explain this difference. The clinical question is therefore about the relative observed outcomes under the two assigned analgesia approaches, not about whether either approach is universally preferable or appropriate for an individual patient.

3. Trial Design

The registry describes a randomized, parallel-group study comparing programmed intermittent epidural bolus with continuous epidural infusion for analgesia during voluntary second-trimester termination of pregnancy. Enrollment is recorded as 104, and the primary and secondary outcome groups each report 52 participants per arm. The study status is completed. The record gives the masking classification as quadruple; its brief summary describes the study as double-blind. It does not clarify the difference between those descriptions.

The primary outcome was incidence of motor block, assessed hourly from the start of the analgesia procedure up to 66 hours. The recorded secondary outcomes were patient satisfaction at hospital discharge, up to 72 hours from the start of the procedure; total levobupivacaine consumption at fetal expulsion, up to 66 hours; and total sufentanil consumption during the analgesia procedure, assessed through 66 hours. These outcomes cover a motor-function event, a patient-reported rating, and medication consumption.

The registry lists the analgesia procedures, pumps, drugs used for analgesia, the termination procedure, and a drug used for the termination procedure among the interventions. It does not provide detailed arm regimens in the arm descriptions. The original design rationale, sample-size justification, randomization procedure, allocation concealment details, and the trial's planned statistical methods are not reported in the registry record. The posted results give outcome summaries and analysis methods, but these do not establish what was specified before the study began. The record also does not give enough information to characterize recruitment, follow-up completeness, or adherence to assigned analgesia.

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 Incidence of Motor Block, measured over Assessed every hour from starting the analgesia procedure (up to 66 hours from starting of the procedure)..

The primary endpoint was incidence of motor block, expressed as the number of participants meeting the registry's definition. Motor function in the right and left lower extremities was assessed with the Breen modified Bromage score. The scale describes degrees of lower-extremity movement and weakness, from complete block to the ability to stand and perform a partial knee bend. A score below 6 was counted as motor block.

Assessments were made every hour from the start of analgesia, for up to 66 hours from the start of the procedure. Thus, the endpoint is a participant-level count of those who met the motor-block criterion during the recorded assessments; it is not a measure of the duration or severity of block. The registry does not explain whether participants with repeated qualifying assessments were counted once or how missing assessments were handled.

As a general measurement point, a binary endpoint can make a clinically observable event easier to compare between randomized groups: each participant is classified as meeting or not meeting the stated criterion. That clarity depends on applying the same definition and ascertainment process across groups. The Bromage threshold gives the endpoint an explicit rule, but collapsing different levels of motor impairment into one event category discards distinctions in severity. The registry names the primary outcome and threshold, but does not report further detail on assessor training or measurement reliability.

7. Results Posted in the Registry

• Programmed Intermittent Epidural Bolus: 5.8% (3/52) versus 46.2% (24/52) on control; risk difference -40.4 percentage points (95% CI -55.3 to -25.4), risk ratio 0.12 (0.04–0.39); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Degree of Satisfaction of the Patients With the Analgesia Procedure

• 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:
  • Programmed Intermittent Epidural Bolus: mean 84.40 versus 73.20 on control; difference 11.20 (95% CI 4.46 to 17.94), standardized effect d = 0.64; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Programmed Intermittent Epidural Bolus than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Total Levobupivacaine Consumption

• 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:
  • Programmed Intermittent Epidural Bolus: mean 75.50 versus 86.20 on control; difference -10.70 (95% CI -21.04 to -0.36), standardized effect d = -0.40; z-test p = 0.043.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Programmed Intermittent Epidural Bolus than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Total Sufentanil Consumption.

• 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:
  • Programmed Intermittent Epidural Bolus: mean 60.40 versus 69.00 on control; difference -8.60 (95% CI -16.88 to -0.32), standardized effect d = -0.40; z-test p = 0.042.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Programmed Intermittent Epidural Bolus than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover patient satisfaction and consumption of two analgesic drugs. Across these outcomes, the posted group summaries have a consistent numerical direction: satisfaction is higher in the programmed intermittent epidural bolus group, while the listed mean consumption values are lower. This overall pattern is broadly aligned with the primary result, in which fewer participants in that group met the motor-block definition. The outcomes nevertheless measure different things and should not be combined into a single claim.

The reported analyses for the secondary outcomes are Wilcoxon (Mann-Whitney) tests, while the summary-statistic recalculations express mean differences. The results are therefore not identical statistical summaries of the same estimand. The posted p-values indicate evidence under their respective tests, but do not quantify clinical importance. The registry does not report thresholds for a meaningful difference in satisfaction or drug consumption, nor does it report confidence intervals from the sponsor's rank-based analyses.

Secondary findings generally carry less weight than a prespecified primary outcome because many outcomes can create more opportunities for chance findings. A multiplicity adjustment or a prespecified hierarchy can address some of this concern, but such a plan is not reported in the registry record. Without that information, the secondary results are best treated as supportive and descriptive rather than as separate confirmatory conclusions. Their consistency with the primary outcome is noteworthy, but it does not remove uncertainty about multiplicity, the analysis methods, or missing observations.

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

• Degree of Satisfaction of the Patients With the Analgesia Procedure
• Total Levobupivacaine Consumption
• Total Sufentanil Consumption.

9. Statistical Interpretation

10. Statistical Methods Explained

Randomization assigns participants to study groups by chance. In general, this helps limit systematic differences between groups at the time of assignment, so an outcome contrast can be interpreted as a comparison of the assigned approaches within the trial. Randomization does not guarantee that every relevant characteristic is balanced, and it does not remove concerns about missing outcomes, deviations from assignment, or differences in outcome assessment. The registry identifies this study as randomized and parallel-group, but does not report the sequence-generation or allocation-concealment methods.

What does the primary risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the comparison group. Here, the reported contrast is programmed intermittent epidural bolus relative to continuous epidural infusion. A negative estimate means the observed proportion with motor block was lower in the intermittent-bolus group. The recalculated estimate is -0.404. Its 95% confidence interval ranges from -0.553 to -0.254. Because the interval remains below zero, the values compatible with this calculation all indicate a lower event proportion in the intermittent-bolus group. This is an unadjusted comparison from the posted group summaries, not an adjusted estimate.

Risk differences are on the absolute scale: they describe the change in event proportion rather than a relative comparison. The registry also gives relative measures, but the risk difference directly communicates the separation in observed event proportions. Any interpretation remains dependent on the endpoint definition, the participants included in the summaries, and the handling of missing assessments. Those analysis details are not reported in the registry record.

What does the chi-squared test assess?

The chi-squared test is a general method for assessing whether categorical outcome distributions differ between groups. For the primary result, the registry reports a chi-squared analysis with p < 0.001. A p-value is calculated under a model in which there is no group association or difference, and indicates how unusual data at least as discrepant as those observed would be under that model and its assumptions. It is not the probability that the no-difference model is true, nor does it express the size or practical importance of the difference. The method and p-value are reported; details of any additional covariate adjustment are not reported.

How should the secondary comparisons be read?

The registry reports means and standard deviations for satisfaction and drug consumption, and reports Wilcoxon (Mann-Whitney) analyses for each comparison. The Wilcoxon (Mann-Whitney) method compares the rank distributions of observations between groups. It is not simply a test of a difference between means, even though means and standard deviations are also posted. The recalculated secondary estimates are unadjusted mean differences derived from the posted summaries. They answer a mean-scale question and should not be treated as identical to the sponsor's rank-based analyses.

For the recalculated mean differences, the confidence interval describes uncertainty in the estimated difference under the assumptions of that calculation. A standard deviation describes variation among participant observations; it is not the same as the standard error, which describes uncertainty in an estimated group mean. General statistical reasoning distinguishes these quantities because a group can have substantial participant-to-participant variation while the estimated mean is more or less precise depending on the available information. The registry supplies means and standard deviations but does not report participant-level distributions.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when outcome variability is greater than a statistical model assumes. If a model understates variability, its standard errors can be too small and its confidence intervals too narrow, making the evidence appear more precise than it is. The posted primary outcome is a binary event count and the registry reports a chi-squared test; it does not report a dispersion assessment or a model-based adjustment for over-dispersion. The concept therefore explains a general issue in statistical modeling, not a documented feature of this trial's analysis.

What can and cannot be inferred from the analyses?

The primary recalculation is a simple, unadjusted comparison of the posted counts. The secondary recalculations use posted means and standard deviations and are likewise unadjusted. These calculations do not replace the registry's own analyses. The registry reports a chi-squared test for the primary endpoint and Wilcoxon (Mann-Whitney) tests for the secondary endpoints. The registry does not report a detailed prespecified statistical analysis plan, adjustment strategy, treatment of protocol deviations, or analysis population definition. Those items should not be inferred from the methods named beside the posted results.

11. Confidence Intervals and Precision

The 95% confidence interval for the recalculated primary risk difference is -0.553 to -0.254. It lies below zero, while still covering a range of possible magnitudes for the group contrast. This interval is evidence about the precision of the estimated difference under the calculation's assumptions; it is not a range containing a guaranteed proportion of individual outcomes, and it does not establish the probability that the true effect lies within those limits.

For the secondary recalculations, the 95% confidence interval for satisfaction's mean difference is 4.459 to 17.94 mm. For levobupivacaine consumption the interval is -21.04 to -0.360 mg, and for sufentanil consumption it is -16.88 to -0.317 microg. These are unadjusted intervals derived from posted summary statistics. They express uncertainty on the mean-difference scale; the sponsor's reported secondary tests are rank-based and do not report confidence intervals in the registry.

As a general explanation, a confidence interval combines an estimate with its sampling uncertainty. Wider intervals indicate less precision about the magnitude, while narrower intervals indicate greater precision under the model used. Precision is not the same as validity: an interval can be calculated precisely around an estimate that is affected by missing data, measurement limitations, or other bias. Nor does an interval by itself establish whether a difference is clinically important. The record does not report a threshold for clinical importance or enough detail to assess how missing observations might affect these intervals.

The interval for the primary comparison does not include zero, and neither do the recalculated intervals for the secondary mean differences. That feature is consistent with evidence against a zero contrast in each unadjusted calculation, but the endpoints are not independent confirmations of one claim. Multiple outcome testing and the difference between recalculated mean-based comparisons and the sponsor's reported rank-based tests both matter when interpreting the secondary findings.

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 events. They are illustrations calculated from the observed effect, rather than the trial's original design assumptions; the original sample-size justification and design assumptions are not reported in the registry record. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. For time-to-event outcomes, the listed convention would be total events, but the outcomes in this trial are not presented as time-to-event planning figures.

The 80% power column describes the illustrative number of participants per arm needed for an analysis to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true one. The 90% power column makes the same kind of planning statement with a higher chance of detection, and therefore generally requires a larger planned sample. The rows show that planning for 75% 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 they require more information, usually through more participants.

These are planning illustrations, not observed power. They do not show the probability that the completed trial's findings are true, and they do not establish that the trial was adequately designed or powered. The calculations use the observed effects, which can be uncertain, and the assumptions may not match the trial's original planning. They are best read as scenarios showing how the required sample size changes when the target effect or desired power changes.

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 = 0.462; treatment proportion p₁ = 0.058; average p̄ = 0.260.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6200 = 1.2152.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5503 = 0.4632.
4. n = (1.2152 + 0.4632)² / (-0.4038)² = 17.3, rounded up to 18 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 <- 0.461538461538462                          # control proportion
p1 <- 0.0576923076923077                          # 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(1860521)
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 = 18 (80% power), 23 (90% power)
 75% of observed effect: n per arm = 36 (80% power), 47 (90% power)
 50% of observed effect: n per arm = 88 (80% power), 117 (90% power)
power.prop.test: 17.3 
Simulated power at n = 18 per arm: 0.841 (20000 replicates)

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

14. Analyses Reported by the Sponsor

For the primary endpoint, the registry reports a chi-squared analysis with p < 0.001. The recalculated unadjusted comparison from the posted counts also gives p < 0.001 and reports the risk difference with a 95% confidence interval. The record marks no discrepancy between the posted result and the recalculation. The sponsor's reported analysis remains the trial's own analysis; the recalculation is a transparent, summary-statistic comparison rather than a replacement for it.

For satisfaction, levobupivacaine consumption, and sufentanil consumption, the registry reports Wilcoxon (Mann-Whitney) tests. The recalculated comparisons use differences between posted means and confidence intervals derived from summary statistics. These methods address related but not identical questions: the rank-based test compares distributions of ranks, whereas the recalculation quantifies a difference in means. Their p-values should not be expected to match exactly or interpreted as if they came from the same test.

The record does not provide enough detail to reconstruct the sponsor's full analysis or determine whether other analysis choices were used. The recalculations are unadjusted and should be viewed as an additional way to describe the posted summaries. Where a discrepancy is flagged, the sponsor's own analysis takes precedence; no discrepancy is flagged for this record.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies motor block as the primary outcome and lists three secondary outcomes. It does not report a multiplicity-adjustment procedure, a testing hierarchy, or a rule for interpreting the family of outcome tests. When several outcomes are tested, the chance of at least one apparently notable result can increase. General statistical approaches may control this risk or distinguish confirmatory from exploratory analyses, but the registry record does not state that any particular approach was used. The secondary p-values should therefore be read as unadjusted evidence for their individual comparisons, not as proof that the overall set of findings meets a prespecified family-wise criterion.

Missing-data handling is not reported in the registry record. The record does not state how incomplete hourly motor assessments were handled, whether all randomized participants were included in each analysis, or whether any imputation or sensitivity analysis was used. It also does not report a definition of the analysis population, such as whether analyses followed assigned group regardless of treatment received. These omissions matter because the meaning of a group comparison depends in part on who contributed outcome data and how missing observations were treated.

The registry provides the arm-level denominators for the posted outcomes, but those summaries alone do not explain whether there were missed assessments, exclusions, or protocol deviations. No assumptions about the reasons for missing data or their likely direction should be made from the reported counts. The original statistical analysis plan, interim-analysis plan, and sample-size justification are not reported in the registry record. Without those details, it is not possible to determine from the posted record whether analysis choices were prespecified or how the investigators intended to manage multiple outcomes and incomplete data.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1.9% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hemorrhage (5.8%), uterine perforation (5.7%).

The adverse-event record lists 3 participants with serious adverse events in each group, with 52 at risk in each group. It also lists other adverse events affecting 33 participants in the continuous epidural infusion group and 21 in the programmed intermittent epidural bolus group, with 52 at risk in each group. These are descriptive counts as recorded; they do not by themselves establish that an event was caused by an analgesia approach.

The registry lists Hemorrhage at 5.8% and Uterine perforation at 5.7% among the top serious adverse-event terms. It does not provide arm-specific attribution for these terms in the posted adverse-event summary. Death counts are not reported in the registry record. The record's adverse-event figures should be interpreted with attention to the distinction between serious events and other events, the available denominators, and the absence of further event-level detail. They do not support a broad safety comparison beyond the recorded counts.

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

The results describe outcomes among participants assigned to two epidural analgesia approaches in a randomized study of voluntary second-trimester termination of pregnancy. In the posted primary endpoint, motor block was recorded less often in the programmed intermittent epidural bolus group than in the continuous epidural infusion group. The reported primary analysis has p < 0.001, and the unadjusted risk-difference interval lies below zero. These findings describe a group contrast in this study under its recorded endpoint definition and observation schedule.

They do not establish that either approach is appropriate for every patient, that the same contrast will occur in other settings, or that motor block is the only outcome relevant to analgesia. The primary measure classifies participants according to whether they met a threshold; it does not describe severity or duration. The secondary results add information about satisfaction and medication consumption, but their interpretation is limited by multiple outcomes and the difference between the sponsor's rank-based analyses and the recalculated mean contrasts.

Statistical evidence is not the same as clinical importance. The registry does not report a threshold for a meaningful change in motor block, satisfaction, or drug consumption. Nor does a small p-value state how likely a treatment claim is to be true. The confidence interval helps describe precision in the estimated contrast, but it cannot address biases or uncertainties that are not captured by the calculation.

The record does not report the original sample-size rationale, missing-data procedures, analysis populations, full treatment regimens, or a detailed prespecified analysis plan. Those gaps limit appraisal of the trial's design and the robustness of the estimates. The posted evidence can be described clearly, but should not be stretched into a universal conclusion or a recommendation for an individual clinical decision.

18. Why This Trial Matters Statistically

This trial illustrates how a binary clinical endpoint can translate a functional assessment into a group comparison. The motor-block definition is explicit: a Bromage score below 6 counted as an event. Reporting the underlying event counts alongside a risk difference and confidence interval makes the observed contrast interpretable on an absolute scale, rather than relying only on a significance test.

It also demonstrates why a p-value is not a complete statistical summary. The reported primary p-value indicates evidence against a no-difference model under the chi-squared analysis, while the risk-difference estimate and its interval convey direction, magnitude, and uncertainty. Each contributes a different piece of information. Neither establishes how important the observed difference is to patients, which requires a meaningful-outcome context not reported in the registry.

The secondary outcomes emphasize the need to distinguish estimands and analysis methods. Posted means can be used for an unadjusted mean contrast, but a Wilcoxon (Mann-Whitney) test is rank-based and does not test exactly the same mean-difference question. Clear interpretation depends on stating which quantity an analysis addresses. The registry's lack of a reported multiplicity plan and missing-data approach also highlights how trial results depend on design and analysis details beyond the numerical outcome summaries.

Finally, the sample-size illustrations show how planning requirements depend on the target effect and desired power, while not revealing the rationale used for the completed study. Separating these post hoc planning scenarios from the original design and from observed results is essential for a sound statistical reading.

19. Limitations

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

Several limitations specific to this record constrain interpretation. The arm descriptions are empty, and the intervention listings do not provide the detailed drug concentrations, dosing schedules, adjustment rules, or criteria for additional analgesia. Without those details, the treatment contrast cannot be fully characterized or reproduced from the registry alone.

The primary outcome was assessed hourly for up to 66 hours, but the record does not explain how repeated positive assessments were converted into the participant-level event count, how incomplete assessments were treated, or whether assessors were trained or blinded in practice. The registry's masking classification is quadruple, while the brief summary calls the study double-blind; the record does not reconcile these descriptions.

The record does not report baseline characteristics, eligibility criteria beyond the population description, participant flow, adherence, protocol deviations, or analysis populations. Missing-data methods, a detailed statistical plan, multiplicity handling, interim analyses, and the original sample-size justification are also not reported. The posted secondary analyses use rank tests, whereas recalculated intervals describe mean contrasts, so those inferential summaries should not be conflated. The adverse-event summary gives counts and selected serious-event terms but limited detail on event timing, attribution, or arm-specific term breakdown. These limitations arise from information not reported in the registry record; they do not demonstrate that any particular issue occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Programmed Intermittent Epidural Bolus Versus Continuous Epidural Infusion for Termination of Pregnancy Analgesia — NCT01860521.
• Registry record last updated 2013-10-28; status last verified 2013-08.
• Results first posted 2013-10-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed randomized parallel-group study of programmed intermittent epidural bolus versus continuous epidural infusion for analgesia during voluntary second-trimester termination of pregnancy. Enrollment is 104. The primary endpoint is incidence of motor block, defined as a Breen modified Bromage score below 6 and assessed hourly for up to 66 hours.

The posted primary counts are 24 of 52 in the continuous-infusion group and 3 of 52 in the intermittent-bolus group. The sponsor-reported chi-squared analysis gives p < 0.001. Secondary outcomes address satisfaction and consumption of levobupivacaine and sufentanil; the registry reports Wilcoxon (Mann-Whitney) analyses. The record does not report the original sample-size rationale, missing-data handling, analysis populations, or multiplicity plan, which limits assessment of the full analysis context.