Immediate Postplacental Insertion of IUDs at Time of Cesarean Delivery: A Randomized Clinical Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Immediate Postplacental Insertion of IUDs at Time of Cesarean Delivery: A Randomized Clinical Trial (NCT01539759), a randomized na study. The primary outcome is IUD Use.

2. Clinical Question

The comparison concerns the timing of IUD placement, not a comparison between the two IUD types. The record does not report results separately by device choice, nor does it state how many participants chose each type. The central statistical question is whether the observed difference in IUD use between the randomized groups is compatible with no difference, and how precisely the registry results estimate that difference. The posted estimates describe the participants included in the outcome counts; they do not, by themselves, explain why any participant was not counted or whether the outcome data were complete for everyone randomized.

3. Trial Design

This was a randomized, parallel-group clinical trial with no masking reported. The trial enrolled 112 participants, according to the registry record. The study began in 2012-03, had primary completion in 2014-08, and is listed as completed. Its sponsor was University of North Carolina, Chapel Hill. The record identifies the study as not applicable for phase.

Participants were women who delivered by cesarean at UNC Women's Hospital and wanted an IUD for postpartum contraception. After consenting, they were randomized to immediate postplacental placement during cesarean delivery or to interval placement at a postpartum visit 4-8 weeks later. After randomization, participants could choose a Mirena® or Paragard® IUD. The design therefore compares two placement strategies while allowing a choice of device within the study.

Data collection was planned at baseline, delivery, the 4-8 week postpartum visit, and follow-up encounters at 3 and 6 months. The primary outcome was IUD use at 6 months postpartum. Secondary outcomes listed in the record include IUD expulsion and women's satisfaction with IUDs. The registry results include an expulsion outcome, but satisfaction results are not reported in the registry record.

The outcome-specific participant counts differ from the enrollment figure: the primary results list 50 participants in the interval group and 48 in the immediate group. The safety results give a separate at-risk count for each group. The registry record does not explain these differences or report the analysis population used for each outcome. Random allocation is a design feature intended to support a fair comparison, but the record does not provide enough information to assess the allocation procedure, adherence, or completeness of follow-up in detail.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as IUD Use, measured over 6 months postpartum.

The primary endpoint measures the number of participants using an IUD at 6 months postpartum. The registry reports this outcome as a count in each randomized group, with the corresponding group size also stated. In the interval-placement group, 32 of 50 participants were recorded as using an IUD; in the immediate-placement group, 40 of 48 were recorded as using one.

This endpoint addresses whether the two placement strategies resulted in different levels of IUD use at the follow-up time chosen by the trial. It is a participant-level outcome: a person is counted according to whether an IUD was in use at that time, rather than according to the number of visits or devices. The registry description does not give a more detailed operational definition, such as how use was confirmed or how missing status was classified; those details are not reported in the registry record.

Use at 6 months is a practical outcome for comparing strategies intended to establish postpartum contraception. It captures the status at a specified follow-up point, but does not describe use at every point between delivery and follow-up. It also does not, by itself, explain why a participant was or was not using an IUD. The endpoint is therefore informative about the reported group outcomes, while its interpretation depends on the outcome definition and follow-up completeness, details that the registry record does not fully provide.

7. Results Posted in the Registry

• Immediate Postplacental IUD Placement: 83.3% (40/48) versus 64.0% (32/50) on control; risk difference 19.3 percentage points (95% CI 2.4 to 36.3), risk ratio 1.30 (1.02–1.66); unadjusted two-proportion z-test p = 0.030.

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.

IUD Expulsion

• 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:
  • Immediate Postplacental IUD Placement: 8.3% (4/48) versus 2.0% (1/50) on control; risk difference 6.3 percentage points (95% CI -2.4 to 15.1), risk ratio 4.17 (0.48–35.96); unadjusted two-proportion z-test p = 0.154.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Immediate Postplacental IUD Placement and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes listed in the record are IUD expulsion and women's satisfaction with IUDs. An expulsion comparison is posted; satisfaction results are not reported in the registry record. Across the available outcomes, the primary endpoint and the expulsion endpoint do not show the same degree of statistical precision. The primary comparison's confidence interval excludes no difference, whereas the expulsion interval includes no difference and spans both lower and higher values for the immediate-placement group.

This contrast matters when interpreting the overall pattern. The primary outcome concerns IUD use at 6 months postpartum, while expulsion is a specific event during the 0-6 month period. They are related in the sense that expulsion may be relevant to continued use, but the posted data do not establish that it explains the primary outcome pattern. These outcomes measure different aspects of the trial and should not be combined into a single conclusion.

The registry includes no reported analyses for the secondary outcomes. In general, secondary outcomes can be useful for describing additional aspects of a trial, but they may be less central to the original question and can involve multiple comparisons. When several outcomes are examined, the chance of at least one apparently notable result can increase unless multiplicity is addressed. Whether the investigators used a prespecified hierarchy or adjustment is not reported in the registry record.

Accordingly, unadjusted secondary results carry less weight than a clearly prespecified primary outcome, especially when their intervals are broad and the analysis plan is unavailable. They can inform what was observed and what remains uncertain, but they should not be treated as independent confirmation of the primary result. The available registry information does not support conclusions about satisfaction or a comprehensive balance across all secondary outcomes.

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

• IUD Expulsion
• Women's Satisfaction With IUDs

9. Statistical Interpretation

10. Statistical Methods Explained

The registry posts a risk difference for the primary binary outcome. A binary outcome places each participant in one of two categories for the measure being assessed: using an IUD or not recorded as using one at 6 months postpartum. The risk, in this context, is the proportion of participants with the outcome in a group. The risk difference subtracts the comparator group's proportion from the intervention group's proportion. A positive estimate therefore indicates a higher observed proportion in the immediate-placement group.

What does the risk difference describe?

The reported risk difference is 0.193. It summarizes the absolute separation between the two posted outcome proportions on the proportion scale. Unlike a relative measure, it does not express one group's outcome as a multiple of the other's. It can be read alongside the group counts and proportions to see both the observed group outcomes and their contrast. The estimate is unadjusted: the record does not report a model adjusting for participant characteristics or other variables.

How should the p-value be read?

The unadjusted p-value is 0.03. In general, a p-value describes how unusual data at least as incompatible with a stated null model would be if that model and the assumptions used for the calculation were correct. It is not the probability that the null model is true, and it does not measure the size or importance of the observed difference. The registry does not report further details of the test or its assumptions, so the posted p-value is best interpreted as the reported unadjusted evidence for the comparison rather than as a complete analysis account.

What does randomization contribute?

In general, random assignment helps make groups comparable at the start of a study, on average, by separating treatment assignment from participants' measured and unmeasured characteristics. That design can strengthen interpretation of a group comparison. It does not guarantee that the outcome groups remain comparable if follow-up or outcome availability differs, nor does it remove uncertainty from a small dataset. The registry identifies the study as randomized, but details of sequence generation, concealment, adherence, and the handling of missing data are not reported in the registry record.

Why do interval estimates matter?

A confidence interval gives a range of effect values that are compatible with the observed data under the method's assumptions. In general, a narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the effect's magnitude. For the primary risk difference, the 95% interval is 0.024 to 0.363. It lies above zero, but it covers a range of possible positive differences; the point estimate should not be mistaken for a precisely known effect.

What do relative measures add?

The registry also posts a risk ratio of 1.302, with a confidence interval from 1.021 to 1.661, and an odds ratio of 2.812, with a confidence interval from 1.084 to 7.3. These measures express the group contrast on relative scales. A risk ratio compares proportions, whereas an odds ratio compares odds, which are the ratio of outcome counts to non-outcome counts within a group. The odds ratio can appear farther from the null value than the risk ratio when outcomes are common. The registry's risk difference remains a direct way to describe the absolute group contrast. Each relative estimate has uncertainty and should not be read as a separate independent finding.

What does over-dispersion mean in general?

Over-dispersion is a concern when the observed variation in data is greater than a statistical model expects. It can arise, for example, when outcomes vary more across individuals or clusters than a simple model assumes. When present and unaccounted for, uncertainty can be understated. The posted primary endpoint is a participant count for a binary outcome, and the registry does not report an over-dispersion assessment or a model that would address it. No claim about over-dispersion in this trial can be made from the record.

The record lists no reported analyses beyond the posted summary comparisons. The trial's statistical analysis plan, the original sample-size justification, any interim analyses, and procedures for adjustment or covariate modeling are not reported in the registry record. These omissions do not show that such procedures were or were not used; they limit what can be concluded from the registry entry alone.

11. Confidence Intervals and Precision

The primary risk difference is 0.193, with a 95% confidence interval from 0.024 to 0.363. The interval does not include zero, indicating that the posted estimate is compatible with a positive difference under the calculation used. Its lower and upper limits nevertheless represent substantially different possible magnitudes, so the precise size of the group contrast remains uncertain.

In general, a confidence interval is not a guarantee that the true effect lies within its limits, nor does it describe the probability that a particular value is true. It is a range constructed using a method that, over repeated use under its assumptions, has a stated coverage property. The registry does not provide details of the interval calculation beyond the posted estimates, and no further assumptions should be inferred.

The relative measures also have intervals: the risk ratio is 1.302, with a 95% confidence interval from 1.021 to 1.661; the odds ratio is 2.812, with a 95% confidence interval from 1.084 to 7.3. The intervals are wide enough to leave uncertainty about the magnitude on those scales. Because risk ratios and odds ratios use different scales, their numerical values should not be compared as though they represented the same quantity. The risk difference directly conveys the absolute separation between the observed proportions.

The interval width should be considered in light of the outcome-specific group counts and the absence of reported information about missing data and analysis populations. The registry does not explain whether all randomized participants contributed outcome data or how any unavailable outcomes were handled. The confidence interval captures sampling uncertainty under its method; it does not resolve uncertainty caused by incomplete reporting, possible selection in the observed outcome group, or limits on generalizing beyond this study.

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 table and curve are planning illustrations based on the observed effect, not a report of the trial's original design calculation. The listed figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect as the effect to detect. The trial's own original sample-size assumptions are not reported in the registry record.

The column for 80% power gives the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. Power is a property of a planned design under assumptions, not a measure of what happened in this completed trial.

The rows consider planning for 100%, 75%, and 50% of the observed effect. Smaller target effects require more participants per arm in these illustrations, because smaller differences are harder to distinguish from sampling variation. The figures are not evidence that the trial was adequately or inadequately sized for its original purpose, since the original justification and target effect are not reported in the registry record. This is not observed power.

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 = 0.640; treatment proportion p₁ = 0.833; average p̄ = 0.737.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6229 = 1.2208.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6077 = 0.5114.
4. n = (1.2208 + 0.5114)² / (0.1933)² = 80.3, rounded up to 81 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 <- 0.64                          # control proportion
p1 <- 0.833333333333333                          # 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(1539759)
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 = 81 (80% power), 107 (90% power)
 75% of observed effect: n per arm = 152 (80% power), 203 (90% power)
 50% of observed effect: n per arm = 360 (80% power), 481 (90% power)
power.prop.test: 80.3 
Simulated power at n = 81 per arm: 0.811 (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 identifies IUD use at 6 months postpartum as the primary outcome and lists IUD expulsion and women's satisfaction with IUDs as secondary outcomes. The registry results include an expulsion comparison, but satisfaction results are not reported in the registry record. The record lists no reported analyses. It does not describe an analysis plan, a hierarchy among outcomes, or any procedure for adjusting for multiple comparisons.

Multiplicity arises when researchers assess more than one outcome, time point, subgroup, or statistical contrast. In general, making many tests can increase the chance of finding a result that appears statistically notable even when there is no underlying effect. Prespecified primary outcomes and transparent adjustment or interpretation strategies can help readers judge the evidence. Since the registry does not report how multiplicity was handled, the unadjusted secondary comparison should be interpreted cautiously; it cannot be treated as though it were the sole planned test.

Information about missing data and analysis populations is also limited. The record gives outcome-specific participant counts for the primary and expulsion results, but does not state whether every randomized participant contributed to each outcome, why the counts differ from the enrollment figure, or how missing outcomes were handled. It does not identify an intention-to-treat, per-protocol, or other analysis population. Those details are not reported in the registry record.

The registry does not describe an interim analysis plan or report whether interim looks at the outcome data occurred. It also does not report the trial's statistical analysis plan, covariate adjustment, or methods for handling protocol deviations. These absences should be understood as reporting gaps, not proof that the procedures were absent. They limit the ability to assess whether the posted analyses match a prespecified plan and how robust the estimates are to missingness or analytic choices.

For these reasons, the primary estimate is best read as the posted unadjusted result with uncertainty about completeness and analytic specification. The secondary estimate adds descriptive context, but the record does not provide enough information to evaluate multiplicity control or the selection of reported analyses.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse event figures for 56 participants at risk in each group. It records 0 serious adverse events in the interval-placement group and 0 in the immediate-placement group. These figures describe the serious adverse event reporting included in the registry; they do not establish that the risk of a serious event is zero. The counts are limited to the populations and reporting period represented in the record, and the record does not give additional detail about serious event definitions or follow-up completeness.

For other adverse events, the record lists 1 affected participant in the interval group and 0 in the immediate group, with 56 at risk in each. These are sparse counts and should be interpreted descriptively rather than as a precise comparison of event risk. The deaths field is not reported in the registry record. The registry does not provide serious adverse event terms, so the nature of serious events cannot be characterized from this entry.

Safety figures are separate from the primary IUD-use outcome. They provide limited information about recorded adverse events but do not, on their own, establish a comprehensive safety profile or explain the overall balance of outcomes between groups.

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

The posted results show a higher observed proportion using an IUD at 6 months postpartum in the immediate-placement group than in the interval-placement group. The estimated risk difference was 0.193, and its 95% confidence interval, from 0.024 to 0.363, was entirely above zero. The unadjusted p-value was 0.03. These statistics describe the observed comparison and its sampling uncertainty under the reported calculation.

They do not mean that every participant assigned to immediate placement used an IUD at follow-up, or that no participants in the interval group did so. The results are group summaries, not predictions for an individual. They also do not identify why the observed proportions differed. The registry record does not report enough detail about outcome confirmation, missing observations, adherence, or the analysis population to resolve those questions.

The primary result does not establish that one IUD type performed differently from another. Participants could choose between Mirena® and Paragard®, but device-specific counts and estimates are not reported in the registry record. The result also does not describe use at every point after delivery; it refers to the specified 6-month postpartum assessment.

The trial's secondary information does not supply a complete explanation of the primary outcome. Expulsion is reported, but satisfaction results are not reported in the registry record. The sparse safety figures are not sufficient to establish a comprehensive comparison of harms. The posted data therefore support a description of the primary group contrast, not a complete account of all factors relevant to choosing a placement strategy.

Finally, a randomized trial can strengthen causal interpretation, but the available registry entry leaves important details unclear, including missing data and analysis procedures. The results should be understood within the setting and participants described in the record. They do not by themselves establish that the same estimates apply in other populations or care settings.

17. Why This Trial Matters Statistically

This trial poses a clear statistical comparison: whether IUD use at 6 months postpartum differs between immediate postplacental placement during cesarean delivery and placement scheduled for a postpartum visit. Random assignment is relevant because it offers a structured way to compare the two timing strategies, rather than relying on participants' choice of timing. The primary endpoint is also a direct participant-level outcome at a stated follow-up point.

The registry presents the group counts, proportions, risk difference, relative measures, confidence intervals, and an unadjusted p-value. This allows readers to distinguish the observed size of the contrast from the uncertainty around it. The confidence interval indicates that the estimate is not a single known value, while the outcome counts show the basis of the group comparison. Reading these together is more informative than relying on statistical significance alone.

The entry also illustrates why outcomes should be interpreted separately. The primary result and the expulsion result address different questions and have different levels of precision. The secondary outcome cannot be treated as a substitute for, or simple explanation of, the primary outcome. The absence of satisfaction results and limited analysis reporting also show how registry records can leave gaps that matter for interpreting a trial's full evidence.

Finally, the planning illustrations make explicit that sample-size calculations depend on assumptions about the target effect and design. They are distinct from the original trial justification, which is not reported in the registry record. Separating planning calculations from observed results helps prevent retrospective power claims from being mistaken for evidence about the trial's success or failure.

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 registry record leaves several trial-specific uncertainties. It describes the randomized comparison but does not give details of sequence generation, allocation concealment, adherence to assigned timing, or deviations from the assigned strategy. No masking was reported. These gaps limit assessment of how assignment was implemented and whether the analyzed groups remained comparable through follow-up.

The primary outcome counts do not account for every participant implied by the enrollment figure, and the registry does not explain the outcome-specific numbers or state how missing data were handled. It also does not identify the analysis population. Without this information, it is difficult to assess whether the posted estimates represent all randomized participants or a subset with available outcome data.

The operational definition and ascertainment method for IUD use are not reported in the registry record. Results are not broken down by IUD type, despite participants being able to choose between Mirena® and Paragard®. Satisfaction is listed as a secondary outcome, but its results are not reported. The registry also does not provide detailed definitions or terms for the safety events.

The statistical analysis plan, original sample-size justification, interim analysis procedures, and multiplicity strategy are not reported in the registry record. Thus, readers cannot assess whether the posted analyses followed a prespecified plan or how the investigators addressed multiple outcomes. The unadjusted estimates should be interpreted with these reporting limitations in view, particularly for secondary outcomes.

The trial concerns women delivering by cesarean at UNC Women's Hospital who wanted postpartum IUD contraception. The registry does not provide further participant characteristics needed to judge how closely the study population resembles other settings. The extent to which these estimates apply beyond the described study population is therefore uncertain.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Immediate Postplacental Insertion of IUDs at Time of Cesarean Delivery: A Randomized Clinical Trial — NCT01539759.
• Registry record last updated 2017-10-13; status last verified 2017-09.
• Results first posted 2015-07-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01539759 is a completed randomized, parallel-group trial sponsored by University of North Carolina, Chapel Hill. It compared immediate postplacental IUD placement during cesarean delivery with interval placement at a postpartum visit 4-8 weeks later among women who wanted postpartum IUD contraception. The record lists enrollment of 112 and no masking.

The primary endpoint was IUD use at 6 months postpartum. The posted counts were 32 of 50 in the interval group and 40 of 48 in the immediate-placement group. The risk difference was 0.193, with a 95% confidence interval from 0.024 to 0.363 and an unadjusted p-value of 0.03. IUD expulsion was also reported as a secondary outcome. Satisfaction results are not reported in the registry record.

The registry does not report the analysis plan, missing-data handling, or original sample-size justification. The posted estimates should be read with those reporting limitations and their confidence intervals in mind.