Treatment of Unfavorable Bleeding Patterns in Contraceptive Implant Users: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Unfavorable Bleeding Patterns in Contraceptive Implant Users (NCT02903121), a randomized phase 4 study. The primary outcome is Total Number of Consecutive Bleeding-free Days in First 30 Days From Day 1 of First Treatment (TX1).

2. Clinical Question

The registry describes a phase 4 randomized trial of treatment for unfavorable bleeding patterns in contraceptive implant users. Its summary explains that bleeding side effects can make the ENG implant unappealing for some users and gives the investigators’ rationale for studying tamoxifen in this setting. The trial’s posted primary outcome focuses on bleeding-free days after the first treatment, rather than on pregnancy prevention or a broader measure of implant use.

The question is specific to this treatment regimen and the first-treatment observation period. A secondary outcome concerns total bleeding-free days over the first 90 day reference period from Day 1 of Treatment 1. The registry record names that outcome, but no result for it is included in the posted outcome details. Thus the available numerical comparison addresses the primary 30-day measure, not every question about bleeding over a longer period or about other outcomes.

3. Trial Design

The registry describes a phase 4, randomized, quadruple-masked, parallel-group trial sponsored by Oregon Health and Science University. It is marked completed. The recorded start date is 2017-01-20, and the primary completion date is 2019-06-05. Enrollment is listed as 109.

The posted primary outcome compares a tamoxifen arm with a placebo arm. Tamoxifen was prescribed orally at 10 mg twice daily for 7 days, starting after 3 consecutive days of bleeding. The placebo regimen was also twice daily for 7 days, with the same stated start condition. The arm results list 55 participants for tamoxifen and 52 for placebo. The primary result is reported as a mean number of consecutive bleeding-free days, with a standard deviation for each arm.

Although the registry classifies the study as quadruple-masked, the roles covered by that masking description are not reported in the registry record. The allocation method beyond the randomized designation, the sequence-generation procedure, and the concealment procedure are also not reported in the registry record. The registry lists tamoxifen (open label) as an intervention, but the posted primary comparison and arm results concern tamoxifen and placebo. Further details about how the open-label intervention fits into the study are not reported in the registry record.

The primary outcome timeframe is Day 1 to Day 30, described as the first 30 days from Day 1 of the first treatment (TX1). A secondary outcome is named for total bleeding-free days over the first 90 day reference period from Day 1 of Treatment 1. Detailed eligibility criteria, participant characteristics, treatment adherence, and the conduct of follow-up are not reported in the registry record. Those omissions limit how fully the study population and treatment delivery can be characterized from the posted 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

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 Total Number of Consecutive Bleeding-free Days in First 30 Days From Day 1 of First Treatment (TX1), measured over Day 1 to Day 30.

The primary endpoint is the total number of consecutive bleeding-free days in the first 30 days from Day 1 of the first treatment. It is reported as a continuous measure in days, using an arm mean and standard deviation. The registry describes the measure as bleeding-free days in the first 30 days.

This endpoint captures the length of time without bleeding during the specified period after treatment begins. Consecutive days are relevant to the stated question because they describe the continuity of a bleeding-free interval, rather than only whether any bleeding occurred. The outcome is specific to the first treatment and its 30-day reference period; it should not be interpreted as a summary of all later bleeding experience.

In general, a continuous endpoint can retain information about the range of measured outcomes and can be compared using the difference between arm means. The posted results give each arm’s mean and standard deviation, along with a mean difference and an interval estimate. The registry does not report the detailed rules used to classify bleeding days, how diary or other measurement data were collected, or how missing daily observations were handled. Those details matter because the endpoint depends on determining which days count as bleeding-free and whether the sequence of days is uninterrupted.

The registry also names a secondary outcome concerning total bleeding-free days over the first 90 day reference period from Day 1 of Treatment 1. That outcome has a different time span and is not interchangeable with the primary measure of consecutive bleeding-free days in the first 30 days.

7. Results Posted in the Registry

• Tamoxifen: mean 18.50 versus 8.70 on control; difference 9.80 (95% CI 4.76 to 14.84), standardized effect d = 0.72; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: it counts bleeding-free days, and the registry reports a mean and standard deviation for each arm. The posted comparison is a mean difference between tamoxifen and placebo. This choice of summary gives a direct contrast in the endpoint’s units, days. The estimated difference of 9.8 days is accompanied by an interval from 4.76 to 14.84 days and an unadjusted p-value of <0.001.

What does a mean difference represent?

In general, a mean is the arithmetic average of observed values in a group. A mean difference subtracts one group mean from another according to a specified comparison. In this record, the posted comparison is tamoxifen relative to placebo, and the means listed for those arms are 18.5 and 8.7 days. The difference is an average contrast, not a claim that each participant had the same change. Differences in individual outcomes can be substantial even when an arm mean is clear.

The standard deviation describes the spread of observations around an arm mean. It is not the uncertainty interval for the mean and is not a measure of the difference between arms. The registry reports standard deviations of 17.0 days for tamoxifen and 8.4 days for placebo. Because the outcome is a count bounded by the observation period and the standard deviation in the tamoxifen arm is relatively large compared with its mean, it is useful to remember that a mean-and-standard-deviation summary may not show the full distribution. The registry record does not report a distribution plot or further distributional summaries in the outcome details.

What does the p-value address?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. The posted value is unadjusted and reported as <0.001. The registry record does not report which other outcomes or comparisons, if any, were included in a prespecified testing strategy, so this p-value should not be taken as a multiplicity-adjusted result.

A small p-value and an estimated difference answer different questions. The estimated mean difference describes the magnitude of the observed average contrast in days; the p-value relates the data to a null comparison under an analysis model. The interval estimate adds information about precision by displaying a range of values compatible with the estimation procedure. The confidence level and detailed estimation method for the posted interval are not reported in the registry record.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It can arise when a simple model does not capture important variation among individuals or when outcome data have a distribution different from the model’s assumptions. For outcomes such as counts or repeated daily measurements, accounting for variability appropriately can affect standard errors, intervals, and tests. This is a general statistical consideration; the registry record does not report that an over-dispersion model was used, nor does it provide a model specification that would establish whether over-dispersion was assessed.

The primary endpoint is a count of consecutive days, but the registry labels the analysis as a continuous measure with a mean parameter and standard deviation. That reporting supports a mean-based interpretation of the posted result. It does not identify whether the investigators used a t-test, a regression model, a nonparametric method, or another approach. The detailed statistical test and any model diagnostics are not reported in the registry record. Readers should not infer a particular method from the format of the summary statistics alone.

What does randomization contribute?

In general, random allocation is intended to make treatment assignment independent of participants’ measured and unmeasured characteristics, on average, before treatment. It can support a causal comparison when allocation is implemented as planned and when follow-up and analysis preserve the benefits of randomization. The registry identifies the study as randomized, but the detailed allocation procedure and the handling of participants after randomization are not reported in the registry record. The result is therefore best described as a randomized-arm comparison rather than as proof that all potential sources of bias were eliminated.

The record also describes the design as quadruple-masked. Masking can reduce the possibility that knowledge of treatment assignment influences participant reports, care, or outcome assessment. The roles covered by the masking designation and whether masking was maintained are not reported in the registry record. These are relevant considerations for an outcome that depends on classifying days as bleeding-free.

The registry lists zero analysis records, while posting a primary outcome comparison. This means detailed analysis entries are not available in the record, even though numerical outcome results are posted. The analysis population, handling of missing observations, treatment of protocol deviations, and any prespecified covariates are not reported in the registry record. These omissions prevent a full reconstruction of the analysis from the posted summary alone.

Planning calculations based on the observed effect are described separately from the trial’s observed result. They are illustrations under stated assumptions, not evidence about the power actually achieved by the completed study. The original sample-size justification and the trial’s own design assumptions are not reported in the registry record. A planning calculation cannot replace those missing design details or resolve uncertainties about analysis methods and missing data.

10. Confidence Intervals and Precision

The posted mean difference is 9.8 days, with an interval from 4.76 to 14.84 days. This interval gives a range of estimates around the observed contrast and is more informative about precision than the point estimate alone. The full interval lies on the positive side of no difference, but the exact confidence level and method used to form the interval are not reported in the registry record.

In general, a confidence interval reflects both the estimated effect and its sampling uncertainty under the procedure used to calculate it. A narrower interval indicates greater precision under that procedure, while a wider interval leaves more uncertainty about the size of the effect. An interval is not a guarantee that the true effect falls inside its endpoints, and it does not describe the range of individual participant outcomes. Individual variability is reflected separately by the arm standard deviations: 17.0 days for tamoxifen and 8.4 days for placebo.

The posted interval is for the mean difference, not for either arm mean in isolation. It should be read alongside the means of 18.5 days in the tamoxifen arm and 8.7 days in the placebo arm. The interval’s positive lower endpoint indicates that the reported estimation procedure places the full range above a null difference. The registry does not state whether the interval accounts for any adjustment, clustering, repeated measurements, or multiplicity; no such features should be assumed.

Precision is also limited by what the record does not describe. The approach to missing outcome observations, the analysis population, and the model or test used are not reported in the registry record. The available interval can be interpreted as the interval attached to the posted comparison, but those absent details prevent an independent assessment of its construction.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. They are illustrations based on the observed mean difference, not the original trial’s sample-size justification. 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 targets the stated fraction of the observed effect. The original design assumptions are not reported in the registry record.

For a planning effect set at 100% of the observed effect, the figures are 30 participants per arm for 80% power and 41 participants per arm for 90% power. For planning at 75% of the observed effect, the figures are 54 participants per arm for 80% power and 72 participants per arm for 90% power. For planning at 50% of the observed effect, the figures are 120 participants per arm for 80% power and 161 participants per arm for 90% power.

In general, power is the probability that a planned study will meet its prespecified statistical criterion when a specified effect is present and the assumptions hold. The 80% column means planning for an 80% chance of detecting that target effect under the stated assumptions; the 90% column uses a higher target chance. Smaller effects need more participants to distinguish them from random variation with the same power and significance level. The figures are not observed power for the completed trial.

The curve represents the same planning relationship across the target effect assumptions: as the effect considered becomes smaller, the participant requirement rises. These calculations are planning illustrations based on the observed estimate, which may itself be uncertain. They should not be read as proof that the original trial was designed for any of these scenarios.

12. 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 9.800; pooled standard deviation σ = 13.524.
2. n = 2 × (1.96 + 0.842)² × 13.524² / 9.800² = 29.9, rounded up to 30 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
delta <- 9.8                      # observed difference in means
sigma <- 13.5240737734076                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2903121)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 30 (80% power), 41 (90% power)
 75% of observed effect: n per arm = 54 (80% power), 72 (90% power)
 50% of observed effect: n per arm = 120 (80% power), 161 (90% power)
power.t.test: 30.9 
Simulated power at n = 30 per arm: 0.788 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record names a primary endpoint and a secondary outcome. The primary endpoint is consecutive bleeding-free days during the first 30 days from the first treatment. The named secondary outcome is total bleeding-free days over the first 90 day reference period from Day 1 of Treatment 1. A numerical result for that secondary outcome is not reported in the registry record.

Multiplicity arises when several outcomes, comparisons, time points, or analyses are tested. In general, conducting multiple tests can increase the chance of at least one apparently unusual result under a global null hypothesis. Prespecified testing hierarchies or adjustment procedures can address that issue, but the registry record does not report a multiplicity plan or adjustment for the posted p-value. The primary comparison’s p-value is explicitly unadjusted. The record does not establish whether the primary outcome was the only confirmatory test or how the secondary outcome was intended to be analyzed.

The registry lists zero analysis records, although it posts a primary comparison. This leaves the detailed analysis plan unavailable in the record. The analysis population, whether all randomized participants were included, the handling of participants with incomplete follow-up, and the approach to missing daily outcome information are not reported in the registry record. The population field for the primary outcome is blank. Consequently, the posted arm counts should not be assumed to identify a particular intention-to-treat or per-protocol population.

In general, missing data can affect both the estimated average and its uncertainty, particularly if the likelihood of missingness is related to treatment assignment or the outcome. No missing-data method, imputation approach, or sensitivity analysis is reported in the registry record. It is therefore not possible to determine from the registry entries whether missingness was absent, limited, or addressed analytically.

Detailed protocol deviations, exclusions, and analysis decisions are also not reported in the registry record. These gaps do not negate the posted result, but they restrict evaluation of whether the statistical analysis followed a prespecified plan and whether alternative reasonable approaches could affect the findings.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the tamoxifen arm, with 55 at risk, and zero in the placebo arm, with 52 at risk. Deaths are reported as zero in both arms. The serious adverse event terms list is empty. These figures describe the safety entries posted in the registry and should not be read as proof that no serious event could occur.

For other adverse events, the record lists 45 affected participants among 55 at risk in the tamoxifen arm and 12 among 52 at risk in the placebo arm. These are counts, not rates calculated over a specified person-time period. The registry entries do not report event types, severity breakdowns, timing, duration, relationship to treatment, or the method used to collect and code these events. The difference in counts alone cannot establish that treatment caused or prevented an event.

In general, safety counts depend on the study’s definitions, observation period, reporting practices, and completeness of follow-up. Those details are not reported in the registry record. The figures should therefore be interpreted narrowly as the posted counts for the stated arms, rather than as a complete characterization of comparative safety.

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

The result is a comparison of the posted mean number of consecutive bleeding-free days in the first 30 days after the first treatment. The tamoxifen arm mean was 18.5 days, and the placebo arm mean was 8.7 days. The posted mean difference was 9.8 days, with an interval from 4.76 to 14.84 days and an unadjusted p-value of <0.001. These statistics characterize the average outcome for the recorded arms and the uncertainty attached to the reported contrast.

The result does not mean every participant experienced the arm average or the estimated difference. The standard deviations—17.0 days for tamoxifen and 8.4 days for placebo—show that outcomes varied within arms. Group summaries do not show how many participants had a particular bleeding pattern, how responses were distributed, or whether individual experiences differed in clinically important ways.

The finding is specific to the study’s regimen, population, primary endpoint, and first 30-day timeframe. It does not by itself answer whether bleeding patterns changed over a longer period, whether the named secondary outcome differed, or how treatment affected other outcomes. A numerical result for the secondary 90 day outcome is not reported in the registry record. The result also does not provide evidence about the comparative safety of the regimens beyond the adverse-event entries posted.

Statistical evidence is not the same as a judgment about importance to participants. The registry does not report a threshold for a meaningful difference, participant preferences, or a measure of satisfaction. Nor does the posted comparison establish the effect of the open-label tamoxifen intervention listed in the registry. The primary comparison concerns the tamoxifen and placebo arms.

Finally, the record does not report the detailed analysis plan, missing-data handling, or analysis population. These omissions limit independent assessment of the result’s robustness. The statistics support a description of the posted comparison; they do not justify broader claims about all implant users, longer-term outcomes, or individual treatment decisions.

16. Why This Trial Matters Statistically

This trial poses a clear statistical question about a measured experience that can vary substantially among individuals: the number of consecutive bleeding-free days after a defined treatment. Using a continuous endpoint allows the comparison to retain information about the length of the bleeding-free interval, while the arm means provide an accessible summary in days. The mean difference is likewise expressed in the outcome’s natural unit.

The reported standard deviations are important context for that average. The tamoxifen arm’s standard deviation is 17.0 days, compared with 8.4 days for placebo. This spread reminds readers that an average contrast does not imply a consistent response for all participants. Statistical interpretation benefits from considering the point estimate, its interval, and the distributional information that is available rather than relying on a p-value alone.

The record also illustrates why a posted comparison and a full statistical report are not the same thing. The result includes a mean difference, interval, and unadjusted p-value, but detailed analysis choices, missing-data methods, and the analysis population are not reported in the registry record. Those details affect how readers evaluate reproducibility, potential bias, and the scope of inference.

The planning illustrations demonstrate how sample requirements depend on the target effect and desired power under stated assumptions. They are based on the observed effect, so they are not a substitute for the trial’s original design rationale. Distinguishing a planning exercise from an observed result is essential when interpreting completed-trial data.

Overall, the study is statistically informative because it reports a direct arm comparison on a defined endpoint and includes an interval estimate. Its value for interpretation is constrained by the limited detail about analysis and follow-up. Both the reported contrast and those reporting gaps matter when judging how far the result can be generalized.

17. 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 report detailed eligibility criteria or baseline characteristics. It is therefore not possible to assess from the registry entries how closely participants represent the broader population of ENG implant users with unfavorable bleeding patterns. The reported enrollment and arm counts describe the recorded study, but do not supply information about recruitment, retention, or representativeness.

The primary endpoint relies on classifying days as bleeding-free and assessing whether those days are consecutive. The rules for defining bleeding, the method of daily measurement, and the handling of incomplete diaries or other missing observations are not reported in the registry record. Such details are particularly relevant to an endpoint built from repeated observations across a fixed period.

The detailed statistical analysis plan is not reported in the registry record. The analysis population, model or test, handling of protocol deviations, and missing-data approach are not specified. The posted comparison is unadjusted, and there is no reported multiplicity procedure. The registry lists zero analysis records, limiting the ability to assess whether the posted analysis followed a prespecified plan.

The registry also lists an open-label tamoxifen intervention, but the registry entries available for the primary result describe the tamoxifen and placebo arms. The relationship between the open-label intervention and the posted comparison is not reported in the registry record. A numerical result for the named secondary outcome over the first 90 day reference period is also not reported.

Finally, the safety information is limited to counts for serious and other adverse events and deaths. Event descriptions, timing, attribution, and follow-up duration are not reported in the registry record. These limitations restrict interpretation of both the primary outcome and the broader benefit-risk profile.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Treatment of Unfavorable Bleeding Patterns in Contraceptive Implant Users — NCT02903121.
• Registry record last updated 2020-07-15; status last verified 2020-07.
• Results first posted 2020-07-07.
• 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.

21. Record Summary

The registry record describes a completed phase 4 randomized, quadruple-masked, parallel-group trial sponsored by Oregon Health and Science University. It lists enrollment of 109, a start date of 2017-01-20, and a primary completion date of 2019-06-05. The primary comparison is tamoxifen versus placebo among ENG implant users with unfavorable bleeding patterns.

The primary outcome is consecutive bleeding-free days during the first 30 days from the first treatment. The reported means are 18.5 days for tamoxifen and 8.7 days for placebo, with a posted mean difference of 9.8 days, an interval from 4.76 to 14.84 days, and an unadjusted p-value of <0.001. The registry also names a secondary 90 day outcome, but its numerical result is not reported in the registry record.

Interpretation is limited by the absence of detailed analysis methods, missing-data handling, and analysis-population information. Safety entries report zero serious adverse events and zero deaths in both arms, alongside other adverse event counts of 45 and 12.