Immediate Versus Delayed Insertion of the Copper Intrauterine Device (IUD) After Medication Abortion: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Immediate Versus Delayed Insertion of the Copper Intrauterine Device (IUD) After Medication Abortion (NCT00737178), a randomized phase 4 study. The primary outcome is Use of the IUD for Contraception at Six Months.

2. Clinical Question

3. Trial Design

This was a phase 4, randomized, parallel-group trial with no masking. Columbia University is listed as the sponsor. The registry record gives an enrollment of 156 and a completed status. The listed study dates are 2008-07 for the start and 2009-10 for primary completion.

Participants were assigned to immediate or delayed copper IUD insertion after medication abortion. The immediate group was assigned insertion at the routine follow-up visit one week after abortion initiation; the delayed group was assigned insertion four to six weeks after initiation. The primary outcome was IUD use for contraception at six months. The outcome description specifies an intention-to-treat comparison according to group assignment, with use assessed by in-person exit interviews and phone interviews.

The posted primary outcome counts are 49 participants using an IUD among 71 in the immediate group and 51 among 85 in the delayed group. These outcome denominators add to the registry enrollment, but the record does not explain participant flow, whether any participants were excluded after randomization, or how missing interview data were handled. Those details are not reported in the registry record.

The registry record lists insertion rates and expulsion and removal rates among the secondary outcomes. The brief description also names pain, bleeding, cramping, insertion difficulty, and use of any birth control at six months. Numerical results for those additional measures are not reported in the registry record. The record does not report details of sequence generation, allocation concealment, or a prespecified statistical analysis plan.

4. Participant Flow and Accounting

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

Before assignment: For both groups, the routine 1 week follow-up visit will confirm a successful medication abortion by passage of gestational sac on sonogram. Endometrial stripe thickness will be also be noted. For both groups a transvaginal sonogram will be performed immediately after IUD insertion to confirm IUD position.

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 Use of the IUD for Contraception at Six Months, measured over 6 months.

The primary endpoint is the number of participants using an IUD for contraception six months after enrollment. It is a binary outcome at the participant level: each participant is classified as using or not using an IUD at that follow-up. The registry describes an intention-to-treat analysis, meaning the comparison is based on assigned group rather than on the timing of insertion actually received. Outcome ascertainment was by in-person exit interviews and phone interviews.

This endpoint addresses whether the assigned timing strategy is associated with IUD use at a clinically relevant follow-up point. It captures more than whether insertion was attempted: an IUD could be inserted and later not be in use at the follow-up assessment. Conversely, the endpoint does not by itself explain why a participant was or was not using an IUD. It does not distinguish among reasons such as not returning for insertion, expulsion, removal, or another circumstance unless those are measured and reported separately.

The observed outcome counts were 49 of 71 in the immediate group and 51 of 85 in the delayed group. The registry record does not give a detailed definition of IUD use beyond the interview-based assessment, nor does it report how unobserved six-month outcomes were classified or handled.

7. Results Posted in the Registry

• Delayed IUD Insertion: 60.0% (51/85) versus 69.0% (49/71) on control; risk difference -9.0 percentage points (95% CI -24.0 to 6.0), risk ratio 0.87 (0.69–1.10); unadjusted two-proportion z-test p = 0.242.

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.

Insertion Rates

• 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: 76.5% (65/85) versus 97.2% (69/71) on control; risk difference -20.7 percentage points (95% CI -30.5 to -10.9), risk ratio 0.79 (0.69–0.89); unadjusted two-proportion z-test p = <0.001.
• 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.

The secondary outcome information adds a different perspective from the primary six-month use endpoint. The overall pattern is that the posted insertion-rate comparison is more clearly separated between assigned groups than the primary comparison of IUD use at six months. These outcomes address different stages: insertion by follow-up is not the same as continued use at six months. A difference at one stage need not translate into a similarly clear difference at a later endpoint.

The registry lists expulsion and removal rates as secondary outcomes, and the study description also names experiences such as pain, bleeding, cramping, and insertion difficulty, along with use of any birth control at six months. Numerical results for those measures are not reported in the registry record. Their absence means the broader set of secondary questions cannot be assessed from the posted results.

Secondary outcomes can help describe how an intervention strategy may relate to different parts of a participant's experience, but they generally carry less weight than a prespecified primary outcome when many outcomes are considered. If multiple tests are examined, the chance of finding at least one apparently notable result can increase. The registry does not report a multiplicity adjustment or a prespecified hierarchy of secondary outcomes. The secondary p-values should therefore be treated as unadjusted evidence, not as definitive confirmation of a broader claim.

The secondary pattern does not replace the primary result, and it should not be used to infer unreported outcomes such as expulsion or removal. Nor does it explain the primary result. The registry does not report participant-level links between whether insertion occurred and whether the IUD was still in use at six months. The most defensible reading is to keep the primary and secondary endpoints distinct and to recognize that the secondary findings provide limited context rather than a complete account of the intervention experience.

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

• Insertion Rates
• Expulsion and Removal Rates

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant is counted as either using or not using an IUD at the six-month assessment. For binary outcomes, a group proportion is the number with the event divided by the number assessed in that group. The posted counts are 49 of 71 in the immediate group and 51 of 85 in the delayed group. This endpoint uses the participant as the unit of analysis; it is not a count of insertion attempts or a measure of time until an event.

What does the risk difference express?

The risk difference compares the outcome proportions by subtraction. The reported recalculation is -0.090 for delayed minus immediate. On this scale, zero corresponds to equal proportions, a negative estimate means the delayed group's proportion is lower, and a positive estimate means it is higher. The risk difference is an absolute contrast on the proportion scale. It is often straightforward to interpret, but its numerical size depends on the outcome proportions in the groups.

How do the risk ratio and odds ratio differ?

The risk ratio compares the proportions directly as a ratio; the odds ratio compares the odds of the outcome. Both are relative measures, but they are not interchangeable and can have different numerical values for the same data. For either ratio, a value of one corresponds to no difference between groups. For the primary outcome, the recalculated risk ratio is 0.869 and the recalculated odds ratio is 0.673. The confidence intervals for both include one. These measures provide alternative descriptions of the same observed contrast, rather than separate tests or separate outcomes.

What does the chi-squared test assess?

The registry reports a chi-squared analysis for the primary outcome, with p = 0.24. In general, a chi-squared test evaluates whether the observed distribution of a categorical outcome across groups is compatible with equal proportions, under the assumptions of the test. A p-value summarizes how unusual results at least as discrepant as those observed would be under a specified null model. It is not the probability that the null model is true, and it does not measure the probability that the finding will replicate.

The unadjusted recalculation from the posted primary counts gives p = 0.242. This is close to the sponsor's reported p = 0.24; the small difference reflects the displayed precision of the reported result and the recalculation from summary counts. The registry does not report a more detailed specification of the sponsor's test beyond identifying it as chi-squared.

How should the confidence interval be read?

A confidence interval describes a range of effect estimates compatible with the observed data under the method used to calculate it. In repeated use of a method under its assumptions, intervals at a stated confidence level have a long-run coverage interpretation; an individual interval is not a probability statement that the true effect lies inside its endpoints. For the primary risk difference, the 95% interval is -0.240 to 0.060. Because it includes zero, it allows both a negative and a positive difference as well as values close to no difference.

The interval and p-value are related ways of expressing uncertainty, but neither replaces interpretation of the effect size. An interval can communicate the range of effects that remains plausible under the analysis, whereas a p-value summarizes evidence against a particular null hypothesis. Neither establishes clinical importance. The registry record does not state a threshold for a difference considered important to participants or clinicians.

Why distinguish assigned treatment from treatment received?

The primary endpoint description calls the analysis intention to treat and says participants are compared according to their immediate or delayed assignment. In general, this approach preserves the randomized comparison and estimates outcomes associated with assignment to a strategy, including departures from the intended schedule. It differs from an analysis based only on participants who received insertion at the assigned time, which can lose the protection of randomization. The record does not report a separate analysis by actual insertion timing.

Randomization supports a comparison of assigned groups when allocation and follow-up are implemented appropriately. The registry identifies the trial as randomized, but details of sequence generation, concealment, adherence, and loss to follow-up are not reported in the registry record. Statistical interpretation therefore depends not only on the formula for a contrast but also on how outcomes were collected and how participants with missing outcomes were treated.

These methods describe the reported binary endpoint and the recalculated unadjusted contrasts. They do not establish that every possible source of bias has been addressed. The registry does not report covariate adjustment for the primary analysis, a prespecified hierarchy for outcomes, or details of handling multiple comparisons. The interpretation should remain tied to the reported analysis and the information available about its conduct.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.090, with a 95% confidence interval from -0.240 to 0.060. This interval is wide enough to include effects in either direction: the point estimate is negative, but the upper endpoint is positive. The interval therefore does not pin down the direction of the underlying difference with confidence. It also includes zero, the value corresponding to equal outcome proportions.

On the relative scales, the recalculated risk ratio is 0.869, with a 95% confidence interval from 0.689 to 1.098, and the recalculated odds ratio is 0.673, with a 95% confidence interval from 0.347 to 1.309. Each interval includes one, the no-difference value for a ratio. The estimates should be read together with their intervals: the point estimates alone give an incomplete account of the uncertainty.

In general, a confidence interval's width reflects both the variability of the outcome and the amount of information available. The primary comparison has outcome denominators of 71 and 85. The registry record does not report a target precision or a difference judged important in advance, so the interval cannot be classified against a prespecified margin for importance from this record alone. Its range indicates that the data are compatible with more than one interpretation of the group contrast.

The sponsor reported p = 0.24, and the recalculated unadjusted p-value is 0.242. Neither value replaces the interval's effect-scale information. The interval is especially useful for recognizing that failure to exclude zero is not proof of exact equality. Equally, a nonzero point estimate does not establish a reliable difference when the uncertainty range includes zero and extends across both directions.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's own original design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. For these binary outcomes, the figures refer to participants per arm, not total events.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect. The 90% power column gives the corresponding planning count for a 90% chance. These are design-planning probabilities conditional on the assumptions and chosen effect; they do not describe the probability that the completed trial found a true effect.

For the primary outcome, planning for 100% of the observed effect gives 442 participants per arm for 80% power and 591 participants per arm for 90% power. Planning for 75% of the observed effect gives 774 and 1,036 participants per arm, respectively. Planning for 50% of the observed effect gives 1,714 and 2,294 participants per arm, respectively. The pattern illustrates a general principle: smaller effects require more participants to detect with the same target power, all else held constant.

The planning values are not observed power. The trial's own original sample-size justification and design assumptions are not reported in the registry record. A displayed planning curve should be read as the relationship between a chosen effect size and the estimated participant requirement under the stated assumptions, not as evidence that the trial did or did not have adequate power for its actual effect.

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 = 0.690; treatment proportion p₁ = 0.600; average p̄ = 0.645.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6767 = 1.3263.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6737 = 0.5670.
4. n = (1.3263 + 0.5670)² / (-0.0901)² = 441.1, rounded up to 442 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 <- 0.690140845070423                          # control proportion
p1 <- 0.6                          # 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(737178)
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 = 442 (80% power), 591 (90% power)
 75% of observed effect: n per arm = 774 (80% power), 1,036 (90% power)
 50% of observed effect: n per arm = 1,714 (80% power), 2,294 (90% power)
power.prop.test: 441.1 
Simulated power at n = 442 per arm: 0.793 (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

The registry reports that the sponsor analyzed the primary comparison with a chi-squared test and obtained p = 0.24. An unadjusted recalculation from the posted summary counts gives a risk difference of -0.090, with a 95% confidence interval from -0.240 to 0.060, and p = 0.242. The recalculated risk ratio is 0.869 and the recalculated odds ratio is 0.673, each with a confidence interval that includes its no-difference value.

The sponsor's p-value and the recalculated p-value are closely aligned, and both indicate that the posted primary counts do not provide strong evidence against equal outcome proportions under the respective test. The recalculation uses only the posted counts and is unadjusted; it is not a substitute for a fuller participant-level analysis or for any analysis details not recorded. The sponsor's own result is the reported trial analysis, while the recalculated measures add effect-scale descriptions of the same comparison.

The registry does not provide a fuller account of the sponsor's statistical model or explain whether other analyses were conducted. No difference between the displayed primary p-values is identified in the record as a discrepancy. Interpretation should distinguish the reported test result from the recalculated effect estimates and should not treat either as proof of equality.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is explicitly identified as IUD use for contraception at six months, and its description specifies an intention-to-treat comparison. The registry also lists secondary outcomes, while the brief study description refers to additional experiences and contraceptive measures. The full prespecified outcome hierarchy and statistical analysis plan are not reported in the registry record. It is therefore not possible to determine from the record whether all outcomes and analyses were chosen before results were known.

Multiplicity arises when several outcomes, time points, or statistical tests are examined. In general, conducting many tests without accounting for their number can make a small p-value more likely to appear by chance. The record does not report a multiplicity correction or explain how the secondary analyses should be interpreted in relation to one another. The secondary results should consequently be treated as exploratory or supportive rather than as a collection of independent confirmations.

The primary endpoint description states that participants were compared according to assigned group, which is consistent with an intention-to-treat approach. However, the registry does not explain how missing interview outcomes were handled, whether all randomized participants contributed data to the outcome counts, or whether any imputation or sensitivity analysis was used. The outcome denominators are 71 in the immediate group and 85 in the delayed group, but those counts alone do not establish the completeness of follow-up or the handling of missing observations.

Details of randomization sequence generation and allocation concealment are not reported in the registry record. Masking is listed as none, so participants and study personnel were not masked according to the record. The registry does not describe whether outcome assessors were masked or how the interview-based outcome was verified. These reporting gaps do not establish that bias occurred, but they limit assessment of potential selection, performance, and ascertainment biases.

The record also does not report a sample-size justification, interim analyses, a stopping rule, or a complete statistical plan. These matters should not be inferred from the observed enrollment or the planning illustrations. The available interpretation is therefore based on the registered design labels and posted outcome counts, with uncertainty about unreported analytic and follow-up procedures.

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 0% reporting threshold.

The registry lists 0 serious adverse events among 71 participants in the immediate group and 0 among 85 participants in the delayed group. It also lists 0 other adverse events among 71 in the immediate group and 0 among 85 in the delayed group. No serious adverse-event terms are listed. These are the posted event counts for the groups and should be read as counts recorded in the registry, not as proof that no adverse experiences occurred.

In general, an observed zero does not establish that the underlying risk is zero. The ability to detect uncommon events depends on the amount and completeness of safety follow-up, and those details are not reported in the registry record. The record also does not report deaths; a numerical death count is not reported in the registry record.

The study description mentions pain, bleeding, and cramping as experiences of interest, but numerical results for those measures are not reported in the registry record. The adverse-event figures alone cannot answer those questions or provide a comprehensive account of tolerability. They should be interpreted narrowly as the event counts posted for the listed adverse-event categories.

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

The primary result is a comparison of IUD use for contraception six months after enrollment among participants assigned to immediate or delayed insertion. The posted counts are 49 of 71 in the immediate group and 51 of 85 in the delayed group. The recalculated risk difference is -0.090, with a 95% confidence interval from -0.240 to 0.060; the interval includes zero. The sponsor's reported chi-squared p-value is 0.24. Together, these results indicate substantial uncertainty about the size and direction of the difference in six-month IUD use.

The findings do not establish that the two timing strategies produce exactly equal rates. A non-significant test is not proof of equivalence, and the registry record does not report an equivalence or non-inferiority margin. The point estimate should also not be treated as a precise estimate of a causal effect without considering the confidence interval, outcome ascertainment, follow-up, and the details of trial conduct that are not reported.

The secondary insertion outcome has a more pronounced observed group contrast, but insertion is not interchangeable with use at six months. The record does not post numerical results for several other outcomes described in the study summary, including expulsion, removal, pain, bleeding, cramping, insertion difficulty, or use of any birth control. The primary result therefore cannot provide a complete account of those outcomes.

This is a description of the posted trial results, not medical advice or a recommendation about IUD timing. The findings apply directly to the trial's assigned groups and reported follow-up. Information about eligibility details, missing-data handling, broader participant characteristics, and full analysis procedures is not reported in the registry record, limiting how far the result can be generalized or interpreted.

18. Why This Trial Matters Statistically

This trial illustrates why the outcome chosen for a comparison matters. Whether an IUD was inserted by follow-up and whether it was being used six months later are related but distinct questions. A timing strategy could have a clearer association with reaching insertion while the later-use comparison remains uncertain. Keeping those endpoints separate prevents a result on one step of care from being treated as an answer to a different question.

It also illustrates the value of reporting effect estimates and confidence intervals alongside p-values. The primary p-value alone does not communicate the range of differences compatible with the data. The risk-difference interval spans negative and positive values, making the uncertainty in the direction and magnitude visible. Relative measures offer another scale, but their confidence intervals likewise include the no-difference value.

The trial is identified as randomized and the primary outcome description specifies intention-to-treat analysis. Those features support a comparison by assigned strategy, while the lack of masking and the absence of detailed reporting on follow-up and missing outcomes make assessment of potential bias more difficult. Registry results are most useful when design, analysis, and participant-flow details are reported alongside the estimates.

Finally, the planning illustrations show how the required number of participants changes with the effect a future study aims to detect. They are not a retrospective verdict on the completed trial. Distinguishing planning assumptions from observed results, and keeping secondary outcomes in context, are important statistical habits for interpreting clinical-trial evidence.

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.

The registry record does not provide detailed eligibility criteria, baseline characteristics, or a fuller description of the study population. This limits assessment of how representative the enrolled participants were and how readily the findings might apply to other settings. The posted enrollment is 156, with outcome denominators of 71 and 85, but participant flow and the reasons for any absent outcome data are not described.

The primary outcome relied on in-person exit interviews and phone interviews. The record does not report the interview schedule in detail, response rates, the handling of conflicting or unavailable responses, or whether outcome assessors were masked. Masking is listed as none, but the record does not specify which study personnel knew assignments. These omissions limit evaluation of possible measurement and follow-up bias.

The record does not report sequence-generation methods, allocation concealment, adherence to assigned timing, actual insertion dates, or crossover between strategies. It identifies an intention-to-treat primary analysis but does not provide a detailed analysis plan, covariate-adjustment strategy, or sensitivity analyses. The original sample-size justification and any interim analyses are not reported in the registry record.

Only some secondary outcome results are posted. Numerical results for expulsion and removal, as well as pain, bleeding, cramping, insertion difficulty, and use of any birth control, are not reported in the registry record. The absence of these outcomes limits interpretation of the broader experience described in the trial summary. Multiplicity procedures are also not reported, so secondary p-values require caution.

Finally, the primary confidence interval includes zero and spans effects in both directions. The registry does not state a threshold for a clinically important difference, so statistical uncertainty cannot be translated into a conclusion about practical importance using the record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Immediate Versus Delayed Insertion of the Copper Intrauterine Device (IUD) After Medication Abortion — NCT00737178.
• Registry record last updated 2014-09-19; status last verified 2014-09.
• Results first posted 2014-09-19.
• 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.

23. Record Summary

The registry describes a completed, phase 4, randomized, parallel-group trial with no masking, sponsored by Columbia University. Enrollment was 156. Participants were assigned to CuT380A insertion one week after medication-abortion initiation or four to six weeks after initiation.

The primary outcome was IUD use for contraception at six months, assessed through interviews and analyzed by assigned group. The posted counts were 49 of 71 in the immediate group and 51 of 85 in the delayed group. The sponsor reported a chi-squared p-value of 0.24. The unadjusted recalculated risk difference was -0.090, with a 95% confidence interval from -0.240 to 0.060.

The registry also posts insertion-rate results. Numerical results for several other outcomes described in the study summary are not reported in the registry record. Missing-data procedures, the original sample-size justification, and a complete statistical analysis plan are not reported.