Postplacental or Delayed Insertion of the Levonorgestrel-releasing Intrauterine Device (IUD) After Vaginal Delivery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Postplacental or Delayed Insertion of the Levonorgestrel-releasing Intrauterine Device (IUD) After Vaginal Delivery (NCT00476021), a randomized na study. The primary outcome is IUD Usage Rate at 6 Months.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel trial comparing two timings of levonorgestrel-releasing IUD insertion after vaginal delivery. One group was assigned to immediate postplacental insertion; the other was assigned to delayed insertion 6-8 weeks after delivery. The intervention is identified as the Mirena device. The study is listed as completed, with phase recorded as not applicable.

The registry lists enrollment as 168. For the primary endpoint, it reports 51 participants in each group. Those endpoint denominators should be read as the denominators used for the posted primary results, not as a complete account of participant flow. How the enrollment figure relates to the primary endpoint denominators is not reported in the registry record. The reasons for any differences, including eligibility, receipt of insertion, follow-up, or analysis decisions, are not reported in the registry record.

The primary outcome was IUD use six months after delivery. The endpoint description specifies that participants lost to follow-up were counted as failures. This rule makes the outcome a combined measure of recorded use and ascertainment: a participant without follow-up is not counted as a successful use outcome under this definition. The registry does not separately report the number lost to follow-up in each group.

Other registered outcomes included whether postplacental insertion was possible, follow-up for delayed insertion, expulsion, infection, and follow-up and unintended pregnancy among participants excluded from postpartum insertion. Quantitative results are posted for expulsion and for pregnancy or follow-up among excluded participants. Numerical results for the other registered outcomes are not reported in the registry record. Details about the randomization procedure, masking, study sites, protocol deviations, analysis populations, and the trial’s 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: IUD use at 6 months, lost to follow-up counted as failures

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 IUD Usage Rate at 6 Months, measured over 6 months after delivery.

The primary endpoint measures whether participants were using the levonorgestrel-releasing IUD six months after delivery. Its unit is participants, and the registry describes the outcome as a number of participants with use. The endpoint is clinically and operationally relevant to the comparison because the strategies differ in when an IUD is intended to be placed, while the outcome asks whether use is present at a later postpartum time point.

The endpoint’s stated population rule matters: participants lost to follow-up were counted as failures. This approach avoids counting missing follow-up as confirmed IUD use, but it also means the outcome reflects both actual use and whether follow-up information was available. Without separate group-specific loss-to-follow-up counts or a different missing-data analysis, the posted endpoint cannot distinguish non-use from unobserved use among those lost to follow-up.

The registry reports 43 participants with use among 51 in the postplacental group and 39 among 51 in the delayed group. It also reports rates of 0.843 and 0.765, respectively, for the contrast as represented in the comparison record. The endpoint does not, by itself, describe the timing or duration of use between delivery and the six-month assessment, nor does it establish why an IUD was not in use. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Delayed IUD Insertion: 76.5% (39/51) versus 84.3% (43/51) on control; risk difference -7.8 percentage points (95% CI -23.2 to 7.5), risk ratio 0.91 (0.75–1.10); unadjusted two-proportion z-test p = 0.318.

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.

Expulsion Rates of Post-placental and Delayed Insertion of the LNG-IUD Using Clinical Exam and Ultrasonography

• 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:
  • Delayed IUD Insertion: 4.3% (2/46) versus 24.0% (12/50) on control; risk difference -19.7 percentage points (95% CI -32.9 to -6.4), risk ratio 0.18 (0.04–0.77); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Delayed IUD Insertion than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Rates of Follow-up and Unintended Pregnancy Rates for Subjects Who Are Excluded From Postpartum Insertion

• 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:
  • Follow-up for IUD Insertion for Ineligible Participants: 26.8% (11/41) versus 4.9% (2/41) on control; risk difference 22.0 percentage points (95% CI 6.9 to 37.0), risk ratio 5.50 (1.30–23.29); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Follow-up for IUD Insertion for Ineligible Participants than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes add context about events and follow-up beyond the primary question of IUD use at six months. Expulsion addresses whether an inserted device remained in place, while the outcomes for participants excluded from postpartum insertion describe pregnancy and later follow-up in a different group. These outcomes relate to the broader study topic, but they do not measure the same endpoint or necessarily concern the same participants as the primary randomized comparison.

The secondary results should not be combined into a single judgment about the primary finding. A difference in expulsion may be relevant to understanding device use, but it does not directly determine whether six-month use differs between assigned insertion strategies. Similarly, outcomes among participants excluded from postpartum insertion inform a population outside the central comparison; they cannot be treated as an additional randomized comparison of postplacental and delayed insertion. The registry record does not report numerical results for every registered secondary outcome, including the named measures of insertion eligibility, delayed-insertion follow-up, and infection.

Unadjusted secondary results carry less weight because testing several outcomes can increase the chance of observing a nominally notable result even when no underlying difference exists. The registry record does not report a multiplicity strategy, a hierarchy for secondary outcomes, or analyses supporting a confirmatory interpretation. The reported p-values can describe the individual comparisons as posted, but should not be read as if each were the sole planned test. Differences in denominators and outcome definitions also matter: they may reflect different analyzed populations or ascertainment, but explanations are not reported in the registry record.

Overall, the secondary outcomes are descriptive evidence about additional aspects of the trial, not substitutes for the primary endpoint. They can motivate questions about retention, follow-up, and outcomes for excluded participants, but the available registry information does not establish how those findings fit into a prespecified inferential plan. The primary and secondary results therefore need to be interpreted separately, with attention to who was included, what was measured, and the uncertainty around each comparison.

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

• Proportion of Women Who Are Able to Have the LNG-IUD Placed Postplacentally and Are Not Excluded From Placement
• Follow-up Rates for Delayed Insertion of LNG-IUD
• Expulsion Rates of Post-placental and Delayed Insertion of the LNG-IUD Using Clinical Exam and Ultrasonography
• Safety of Postplacental Insertion of the LNG-IUD as Measured by Infection Rates
• Rates of Follow-up and Unintended Pregnancy Rates for Subjects Who Are Excluded From Postpartum Insertion

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

A risk difference compares the proportion with an outcome in one group with the proportion in another. Its sign depends on the order of the groups in the contrast. For the primary endpoint, the registry defines the comparison as delayed insertion relative to postplacental insertion, so the estimate of -0.078 points toward a lower recorded use rate in the delayed group. A value of zero would represent equal proportions under that contrast. The interval from -0.232 to 0.075 crosses zero, so the posted data are compatible with differences on either side of equality.

The comparison record also reports a risk ratio of 0.907, with an interval from 0.748 to 1.1, and an odds ratio of 0.605, with an interval from 0.224 to 1.634. These are alternative ways of expressing the contrast, not additional independent outcomes. A risk ratio compares proportions directly; an odds ratio compares the odds of an outcome. Both can be harder to interpret intuitively than a difference in proportions, and the odds ratio should not be read as though it were a risk ratio. Their intervals also span the null values for those measures, consistent with substantial uncertainty in the primary comparison.

What does the p-value contribute?

The primary unadjusted p-value is 0.318. In general, a p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions were correct. It is not the probability that the null hypothesis is true, nor the probability that the observed result occurred by chance in a broader everyday sense. It also does not show whether an effect is clinically important. The confidence interval supplies a more direct view of the range of estimates compatible with the data under the interval’s assumptions.

The registry identifies the p-values as unadjusted. This means they are not reported as corrected for testing multiple outcomes or contrasts. The record does not report the number of planned tests, a hierarchy among secondary endpoints, or a multiplicity procedure. When many outcomes are examined, the chance of at least one apparently unusual result can increase. This general concern is relevant when interpreting the secondary findings, particularly because the registry does not report a prespecified adjustment strategy.

How should the count outcomes be read?

The primary endpoint is binary at the participant level: each participant is counted according to whether use was recorded at six months, with loss to follow-up classified as failure. The displayed counts and denominators therefore summarize participants with the defined outcome in each group. The registry also reports rates for the primary comparison. They are descriptive summaries; the uncertainty around the treatment contrast is represented separately by the confidence interval.

For expulsion, the record reports 12 participants among 50 in the postplacental group and 2 among 46 in the delayed group. The corresponding risk difference is -0.197 for delayed versus postplacental insertion, with an interval from -0.329 to -0.064 and an unadjusted p-value of 0.006. The denominators differ from the primary endpoint denominators. Why they differ is not reported in the registry record. The result should therefore be read using its own outcome-specific denominators rather than assumed to include exactly the same analyzed participants as the primary outcome.

For the record concerning participants excluded from postpartum insertion, the two entries are pregnancy within six months and follow-up for IUD insertion. Each has a denominator of 41, and the posted counts are 2 and 11, respectively. These entries describe different outcomes, not two randomized treatment arms. The registry’s comparison fields report a risk difference of 0.220, with an interval from 0.069 to 0.370 and an unadjusted p-value of 0.007, but the different outcome labels make that contrast unsuitable for interpretation as the primary randomized comparison. The registry does not explain the construction or intended interpretation of that comparison.

What does a confidence interval represent?

In general, a confidence interval is a range produced by a method that, over repeated applications under its assumptions, would cover the underlying parameter at the stated confidence level at the corresponding rate. It is not a range containing a fixed probability that the true value lies inside it after the data have been observed. The width of an interval reflects both the amount of information and the variability in the data, along with the method used to calculate it. Broad intervals indicate less precision than narrow intervals.

For the primary risk difference, the interval extends from -0.232 to 0.075. Because it includes zero, the estimate does not clearly separate a difference in one direction from a difference in the other. This is not evidence that there is no difference; it is evidence that the trial’s posted estimate is imprecise enough to leave multiple interpretations compatible with the data. The registry does not report adjusted analyses or alternative interval methods.

What is not established by the record?

The registry provides a randomized design label and outcome summaries, but does not report enough information to assess every analysis assumption or implementation detail. The method used to generate allocation, who was masked, the analysis population, protocol deviations, missing-data sensitivity analyses, and the original sample-size planning assumptions are not reported in the registry record. The posted calculations cannot answer those questions. The registry’s own analysis should take precedence over simple recalculations from summaries if a discrepancy is reported; the record does not flag a discrepancy for these results.

11. Confidence Intervals and Precision

Precision is best judged from the confidence interval as well as the point estimate. For primary six-month use, the registry reports a risk difference of -0.078 for delayed versus postplacental insertion, with a 95% confidence interval from -0.232 to 0.075. This range crosses zero and spans values in both directions. It therefore leaves considerable uncertainty about the size and direction of the difference. It does not establish equivalence, because no equivalence margin or equivalence analysis is reported in the registry record.

The relative-effect summaries tell a compatible story: the primary risk ratio is 0.907, with an interval from 0.748 to 1.1, and the odds ratio is 0.605, with an interval from 0.224 to 1.634. Both intervals include their respective null values. These estimates are alternative representations of the same comparison, and their numerical scales differ; they should not be treated as separate confirmations.

The expulsion estimate is more clearly separated from zero in its posted interval, which runs from -0.329 to -0.064 for delayed versus postplacental insertion. Its unadjusted p-value is 0.006. That interval indicates a more directional estimate for this secondary outcome, but the result remains subject to the limitations of a secondary, unadjusted comparison. The record does not report an adjustment for testing multiple outcomes.

For the excluded-participant outcomes, the reported risk-difference interval is from 0.069 to 0.370. Its meaning is limited by the different outcome labels in the comparison, which are not a conventional randomized treatment contrast. Confidence intervals quantify statistical uncertainty under an analysis; they do not address bias from missing data, outcome definitions, or other study limitations. Information about those issues is incomplete in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the original trial’s design calculation. The registry record specifies a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculations consider detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

For the primary comparison, the planning figures are participants per arm for 80% power and participants per arm for 90% power. At 100% of the observed effect, the figures are 402 and 537; at 75%, they are 687 and 919; at 50%, they are 1,483 and 1,984. These are planning values for each arm, not combined totals. The non-time-to-event outcomes use participants per arm; the general convention for time-to-event displays is a total number of events, but the listed outcomes are participant-count outcomes.

Power is the long-run probability that a study would meet its specified statistical criterion if a particular effect were truly present and the planning assumptions held. The 80% column represents a design targeting an 80% chance of detecting its chosen effect; the 90% column represents a higher target. In general, smaller effects are harder to distinguish from random variation and require more participants for the same power target. That pattern is visible in the increasing figures as the assumed effect is reduced.

These calculations are illustrative and depend on treating the observed effect as a planning reference. The observed effect can be uncertain, and a future study could have a different underlying effect or different design constraints. The figures are not observed power: they do not measure the probability that this completed trial’s result is correct or explain its outcome.

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 = 0.843; treatment proportion p₁ = 0.765; average p̄ = 0.804.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5615 = 1.1005.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5587 = 0.4702.
4. n = (1.1005 + 0.4702)² / (-0.0784)² = 401.1, rounded up to 402 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 <- 0.843137254901961                          # control proportion
p1 <- 0.764705882352941                          # 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(476021)
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 = 402 (80% power), 537 (90% power)
 75% of observed effect: n per arm = 687 (80% power), 919 (90% power)
 50% of observed effect: n per arm = 1,483 (80% power), 1,984 (90% power)
power.prop.test: 401.1 
Simulated power at n = 402 per arm: 0.800 (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 record lists a primary endpoint and multiple secondary outcomes, but does not report how the investigators planned to handle multiplicity. In particular, it does not describe a testing hierarchy, family of hypotheses, adjustment procedure, or distinction between confirmatory and exploratory secondary analyses. The posted comparison p-values are unadjusted. When several outcomes are tested, the chance of at least one small p-value can be greater than for a single prespecified test. This general issue means that secondary p-values should be interpreted cautiously and should not be treated as independent confirmation of the primary result.

Missing-data handling is specified for the primary outcome only in one respect: participants lost to follow-up were counted as failures for six-month use. The registry does not report how many participants were lost in each group, whether missingness differed between groups, or whether sensitivity analyses examined alternative assumptions. Counting loss to follow-up as failure defines the endpoint analysis, but does not establish what use would have been among participants whose status was unobserved. The handling of missing information for secondary outcomes is not reported in the registry record.

The analysis populations are also not described in enough detail to establish whether the primary results follow an intention-to-treat, per-protocol, or other population definition. The registry reports an enrollment of 168 and primary endpoint denominators of 51 in each group, but does not explain the relationship between them. The expulsion denominators are 50 and 46, and the reason for those denominators is not reported. Participant flow, exclusions after randomization, adherence, protocol deviations, and the handling of these issues in analysis are not reported in the registry record.

These gaps limit the ability to assess whether the posted comparisons preserve the benefits of randomization or how robust they are to alternative analysis choices. They do not prove that the analyses were inappropriate; they mean that the registry record does not provide the information needed to evaluate those aspects. The primary result remains interpretable as the posted estimate under its stated outcome rule, while its broader inferential strength depends on details that are not reported.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death (2.0%).

The adverse-event record reports serious events affecting 1 participant among 51 at risk in the postplacental group and 0 among 51 at risk in the delayed group. Other adverse events are reported for 3 participants among 51 at risk in the postplacental group and 0 among 51 at risk in the delayed group. These counts describe what is posted; they do not establish a comparative safety effect. With few events, estimates of between-group differences would be imprecise, and no adverse-event comparison or confidence interval is reported.

The serious-event term listing includes “death” at 2.0%. The registry record does not provide enough context in the posted information to connect that term to the group-level serious-event counts or explain its coding. The deaths field is not populated for either group, so death counts are not reported in the registry record. The record also does not give event narratives, timing, severity definitions, relatedness assessments, or an explanation of the difference between the term listing and the group summaries. These entries should therefore be read as limited adverse-event reporting rather than a complete safety assessment.

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

The primary result estimates the difference in six-month IUD use under two assigned insertion timings. The point estimate favors postplacental insertion in the direction of the contrast, but the confidence interval includes zero and spans values in both directions. The data therefore do not precisely establish the size or direction of a difference in this endpoint. They also do not establish that the strategies are equivalent or interchangeable; the registry record does not report an equivalence or noninferiority design.

The endpoint is defined with loss to follow-up counted as failure. As a result, the posted comparison concerns recorded six-month use under that rule, rather than a fully observed measure of use for every participant. The registry does not report group-specific loss-to-follow-up counts or analyses using alternative missing-data assumptions. Readers should not interpret the endpoint as separating non-use from unknown use among those without follow-up.

The expulsion result is a secondary finding with an unadjusted p-value. It concerns a separate outcome, has denominators that differ from those for the primary endpoint, and is not a replacement for the primary comparison. The outcomes among participants excluded from postpartum insertion concern a separate population and differently labeled measures. They should not be generalized to the randomized comparison as though they were treatment-arm results.

The registry record supports a description of the trial design, posted outcome counts, and the uncertainty attached to the primary comparison. It does not provide enough detail to assess all aspects of participant flow, analysis populations, missing-data sensitivity, multiplicity, or the original design assumptions. Accordingly, the findings are best understood as estimates from this completed trial, with meaningful uncertainty and reporting limitations. They do not establish a universal result for all postpartum settings, and they do not, on their own, resolve questions that were not measured or reported.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to evaluate a strategy whose intended timing differs, while the outcome is measured later. The primary endpoint is not simply whether insertion was attempted immediately or at a later visit; it is whether IUD use was recorded six months after delivery. That distinction makes the outcome relevant to the overall sequence of placement and continued use, while also combining several possible pathways to the observed result.

The rule that lost-to-follow-up participants count as failures is especially important. It gives missing follow-up a definite role in the endpoint, rather than leaving it outside the definition, but means that follow-up and use are intertwined in the reported outcome. The absence of separate loss-to-follow-up counts prevents readers from seeing how much the result depends on that rule. This is a general lesson in clinical-trial interpretation: an outcome definition can determine what the estimate represents.

The comparison also illustrates why a point estimate should not be read alone. The primary risk-difference estimate has a confidence interval that crosses zero and extends in both directions. The posted counts are informative, but the uncertainty interval shows that they do not pin down a precise comparative effect. A nonsignificant p-value is not proof of equality, and a secondary p-value cannot compensate for uncertainty in the primary endpoint, especially when multiplicity handling is not reported.

Finally, the secondary measures address connected but distinct questions: expulsion, pregnancy, and follow-up among participants excluded from postpartum insertion. Keeping those populations and outcomes separate helps avoid overgeneralizing one result to another. The record demonstrates why statistical interpretation depends on endpoint definitions, denominators, missing-data rules, and the planned role of each analysis, not only on whether an individual p-value is small.

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 reported for this trial. First, the primary endpoint uses 51 participants per group, while enrollment is listed as 168. The registry does not explain the relationship between these figures or report a participant-flow account. The primary denominators therefore cannot be assumed to represent every enrolled or randomized participant.

Second, loss to follow-up was counted as failure for the primary outcome, but the number lost in each group and the reasons for missing follow-up are not reported. This prevents assessment of whether the missing-data rule could have affected the comparison differently across groups. The expulsion outcome uses denominators of 50 and 46, and the reason those denominators differ from one another and from the primary endpoint is not reported.

Third, the registry does not report the randomization procedure, the identity of the masked party, analysis populations, protocol deviations, or sensitivity analyses. It also does not report the original sample-size justification. The planning illustrations based on observed effects should not be mistaken for the trial’s own design assumptions.

Fourth, the secondary comparison for participants excluded from postpartum insertion lists pregnancy and follow-up as its two outcome labels. The registry does not explain the intended interpretation of a risk difference comparing these differently named outcomes, so it should not be read as a randomized treatment contrast. The record also does not report numerical results for all named secondary outcomes.

Finally, the adverse-event reporting is limited: the registry gives group-level counts and a serious-event term listing but does not report event narratives, timing, relatedness, or the deaths field. These gaps restrict interpretation of safety and do not support a complete characterization of adverse events.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Postplacental or Delayed Insertion of the Levonorgestrel-releasing Intrauterine Device (IUD) After Vaginal Delivery — NCT00476021.
• Registry record last updated 2016-06-24; status last verified 2016-05.
• Results first posted 2016-02-19.
• 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 describes a completed randomized, single-masked, parallel trial of immediate postplacental versus delayed levonorgestrel-releasing IUD insertion after vaginal delivery. Enrollment is listed as 168. The primary endpoint is IUD use six months after delivery, with participants lost to follow-up counted as failures.

The primary results report use in 43 of 51 participants in the postplacental group and 39 of 51 in the delayed group. The risk-difference estimate for delayed versus postplacental insertion is -0.078, with a 95% confidence interval from -0.232 to 0.075 and an unadjusted p-value of 0.318. The interval leaves uncertainty about the size and direction of the difference.

Secondary records address expulsion and outcomes among participants excluded from postpartum insertion. Their populations and definitions differ from the primary comparison, and the posted p-values are unadjusted. The registry does not report the original sample-size assumptions, analysis populations, multiplicity plan, or several details needed to assess missing data and participant flow.