Management of Etonogestrel Subdermal Implant-related Bleeding: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Management of Etonogestrel Subdermal Implant-related Bleeding (NCT01658995), a randomized phase 3 study. The primary outcome is Secondary Treatment.

2. Clinical Question

This is a question about a treatment decision recorded after the initial course, rather than a direct measurement of bleeding frequency, duration, or severity. The registry identifies the outcome as the count of participants requesting additional treatment, so the comparison concerns the proportion of participants with that event in each randomized group.

The registry also lists subject satisfaction and removal of the implant as secondary outcomes. Those outcomes provide related but distinct information: satisfaction reflects participants’ views at the specified follow-up, while implant removal records a subsequent decision. Neither is interchangeable with the primary outcome of requesting further treatment.

The trial record identifies the condition as ESI-related bleeding and describes a prospective, randomized, placebo-controlled study in US women. It does not report additional eligibility criteria or a fuller description of the study population, so the question should be interpreted for the enrolled participants described in the registry rather than generalized to groups whose characteristics are not recorded.

3. Trial Design

The registry describes a prospective, randomized, placebo-controlled, parallel-group Phase 3 trial with an enrollment of 82. It lists doxycycline and placebo as the interventions. The arm descriptions indicate that participants were randomized after dissatisfaction with bleeding after 13 weeks post-implant insertion, and that each group received a 10-day course. The doxycycline arm received 100 mg oral capsules twice daily; the placebo arm is described with matching capsule strength and schedule.

After the initial 10-day treatment, participants could request subsequent treatment. The primary outcome timeframe extends from after initial treatment up to 39 weeks. The satisfaction outcome is recorded at 13 weeks post-treatment, and implant removal is recorded at 26 weeks post-randomization. These timeframes differ, so the outcomes represent events assessed at distinct points in follow-up rather than a single common assessment.

The registry classifies masking as triple, while the brief summary calls the trial double-blinded. Both descriptions indicate masking, but the record does not explain the difference in terminology or specify which roles were masked. The protocol’s detailed allocation procedures and the identities of masked groups are not reported in the registry record.

The record lists the Mayo Clinic and Mayo Clinic Health System as the intended trial setting. It gives the status as completed and records an enrollment of 82. The original sample-size justification, the exact schedule of follow-up contacts, and any planned interim analyses are not reported in the registry record. The posted outcome counts are the basis for interpreting the comparisons, but the record does not provide further detail on participant flow or analysis populations.

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 Secondary Treatment, measured over After initial treatment up to 39 weeks.

The registry-designated primary outcome is the number of participants requesting additional secondary treatment of the intervention after the initial treatment. Its timeframe is after initial treatment up to 39 weeks. In practical terms, the event is a request for another treatment after the initial 10-day course; the endpoint does not itself describe the amount of bleeding, how long bleeding continued, or a clinical rating of bleeding severity.

This outcome is useful for representing whether participants sought further intervention during follow-up. It captures a treatment-related decision that can matter to participants and clinicians, while remaining a different kind of measure from a symptom scale or a direct biological measurement. A request may reflect a participant’s experience and preferences, but the registry does not report the reasons for individual requests or the criteria used to classify a request as an event.

The posted results give participant counts for each arm. The doxycycline group had 20 participants with the event among 42, and the placebo group had 23 among 40. The comparison is therefore a difference in observed event proportions. The registry reports a risk difference with a 95% confidence interval and a Chi-squared analysis. Interpretation should focus on the outcome as defined and on the uncertainty around the between-group difference, rather than treating the result as a complete account of all aspects of bleeding or treatment experience.

7. Results Posted in the Registry

• Post ESI Implant - Doxycycline: 47.6% (20/42) versus 57.5% (23/40) on control; risk difference -9.9 percentage points (95% CI -31.4 to 11.6), risk ratio 0.83 (0.55–1.25); unadjusted two-proportion z-test p = 0.370.

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.

Subject Satisfaction

• 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:
  • Post ESI Implant - Doxycycline: 44.1% (15/34) versus 51.5% (17/33) on control; risk difference -7.4 percentage points (95% CI -31.3 to 16.5), risk ratio 0.86 (0.52–1.42); unadjusted two-proportion z-test p = 0.544.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Post ESI Implant - Doxycycline and the control. The interval gives the range of effects that remain compatible with the data.

Removal of ESI

• 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:
  • Post ESI Implant - Doxycycline: 9.5% (4/42) versus 5.0% (2/40) on control; risk difference 4.5 percentage points (95% CI -6.6 to 15.7), risk ratio 1.90 (0.37–9.83); unadjusted two-proportion z-test p = 0.432.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Post ESI Implant - Doxycycline and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address different aspects of the experience after treatment: satisfaction and implant removal. Together, they extend the outcome picture beyond requests for additional treatment, but they do not measure the primary endpoint again. Their timeframes and definitions differ, and the satisfaction denominators are smaller than the primary endpoint denominators. As a result, the secondary findings should be understood as additional, outcome-specific information rather than as a single combined verdict.

Across the secondary outcomes, the posted estimates are uncertain and do not establish a clear between-group difference. The registry-reported satisfaction test has p = 0.46, while its posted recalculation also has an interval spanning no difference. The removal comparison likewise has an interval spanning no difference, and the registry does not post a sponsor analysis for that outcome. These patterns are consistent with the uncertainty in the primary result: they do not provide a decisive contrary signal, but neither do they show that the groups are equivalent.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis because multiple outcomes create more opportunities for an apparently noteworthy result to occur by chance. In general, a multiplicity strategy may control the interpretation of several statistical tests, but the registry record does not report whether one was planned or used. It also does not report a hierarchy for the secondary outcomes. Accordingly, secondary p-values and estimates should be treated as exploratory or supportive evidence unless fuller trial documentation establishes their prespecified status and analysis approach.

The secondary findings should not be combined informally into a claim that treatment did or did not affect overall experience. They concern separate events and measures, and the record does not provide a composite outcome or a joint analysis. Their main contribution is to show that the available follow-up information includes participant satisfaction and implant removal, while leaving substantial uncertainty about the between-group contrasts.

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

• Subject Satisfaction
• Removal of ESI

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is between two randomized parallel groups: doxycycline and placebo. For a binary outcome, each participant either has the recorded event or does not. The arm-level results are counts of participants with the event and the number of participants in each arm. The primary outcome is a request for additional treatment, so the relevant summary is the proportion of participants with that request in each group.

What does a risk difference express?

A risk difference subtracts the event proportion in the comparator group from the event proportion in the intervention group. It is an absolute contrast, rather than a relative measure. A negative value in this comparison indicates a lower observed event proportion in the doxycycline group; a positive value indicates a higher observed event proportion. The sponsor reports the primary contrast as -9.9, and the recalculation gives -0.099. These are presentations of the contrast on different scales, not separate outcomes.

Absolute differences can help describe how far apart the observed event proportions are, but they do not by themselves show how precise the estimate is. The confidence interval supplies information about that uncertainty. The primary interval runs from -31.4 to 11.6 in the sponsor’s report. Because it includes zero, the data are compatible with no difference as well as with differences in either direction under the analysis used.

What is the role of the Chi-squared test?

The registry lists a Chi-squared analysis for the primary comparison. In general, a Chi-squared test assesses whether the observed distribution of a binary outcome across groups is compatible with no association between group and outcome, under the test’s assumptions. The reported p-value is 0.37. A p-value is not the probability that the treatment has no effect, and it does not measure the size or practical importance of a difference. It describes how compatible the observed data are with a specified null model, according to the test.

The posted recalculation is an unadjusted calculation from the arm-level summary statistics. It does not account for covariates or apply an adjustment for other analyses. The registry-reported analysis should be distinguished from that recalculation: the sponsor reports a risk difference, confidence interval, and Chi-squared p-value, and those reported results are the primary reference for the sponsor’s analysis. The recalculated values closely match the posted primary analysis.

How should relative measures be understood?

Relative risks and odds ratios compare groups on relative scales, while the risk difference compares event proportions on an absolute scale. A relative measure can look different in magnitude from an absolute measure because each uses a different reference. They do not change the underlying event counts. For the primary outcome, the posted relative risk is 0.828 with an interval from 0.547 to 1.253, and the posted odds ratio is 0.672 with an interval from 0.281 to 1.606. Each interval includes its null value, consistent with uncertainty about the direction and size of a group difference. The registry’s reported primary analysis is the risk difference, so interpretation should give that sponsor-reported result priority rather than selecting the measure that appears most favorable.

What does a confidence interval add?

A confidence interval gives a range of estimates compatible with the observed data under the method used. In general, it reflects both the point estimate and its sampling uncertainty. A wide interval indicates that the data do not pin down the contrast closely. It does not mean that every value in the interval is equally likely, and it is not a prediction interval for an individual participant. The primary confidence interval spans values on both sides of zero, so the direction of the underlying difference is not determined by these data with high precision.

What can and cannot be inferred from the design?

Randomization is intended to make the assigned groups comparable at baseline on average, but the registry does not report baseline characteristics or details of the randomization procedure. The parallel design means participants were assigned to one of the two treatment groups rather than crossing between treatments. The record says the trial was placebo-controlled and masked, but the description of masking differs between the structured classification and brief summary. The roles masked and procedures for maintaining masking are not reported in the registry record.

The trial record does not report the prespecified statistical analysis plan, the original sample-size justification, handling of missing data, or an analysis-population definition. Those details matter when interpreting outcome-specific denominators and assessing whether the posted analysis followed the original plan. No conclusion about unreported analytic choices should be inferred from the reported Chi-squared result alone.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of -9.9 with a 95% confidence interval from -31.4 to 11.6 in the sponsor’s analysis. This interval includes zero, the value corresponding to no difference in observed event proportions. It also extends in both directions, so the data do not determine whether the event proportion was lower or higher with doxycycline. The point estimate is only one part of the result; the interval communicates the uncertainty around it.

The interval is broad relative to the scale of the estimate, reflecting limited precision in this comparison. In general, precision depends on the amount of information in the data and the variability of the outcome. With binary outcomes, the counts of participants and events contribute to that information. Here, the primary comparison uses 42 participants in the doxycycline group and 40 in the placebo group, with 20 and 23 events, respectively. The registry does not report a precision target or a clinically important difference against which to judge the interval.

The recalculated interval, -0.314 to 0.116, conveys the same uncertainty on the risk-difference scale used by that calculation. The recalculated interval should not be mistaken for a more definitive result: it is an unadjusted reconstruction from posted summary statistics and closely corresponds to the sponsor-reported result. The sponsor’s reported analysis remains the key reported analysis.

Confidence intervals are not a guarantee that the true value lies within a particular range, nor do they assign a probability to each possible effect. In general, a 95% confidence interval comes from a procedure designed to cover the true parameter at the stated rate over repeated uses of the procedure under its assumptions. For these data, the practical message is that a range of potentially relevant differences remains compatible with the observed results. The absence of a statistically clear difference does not establish equivalence, and the interval does not show that all plausible effects are small.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants, for each stated power target. They are illustrations based on the observed effect and use the assumptions listed for this calculation: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning rows consider an effect equal to 100%, 75%, or 50% of the observed effect. For this binary outcome, the figures describe participants needed in each arm under those assumptions; the sample-size convention for time-to-event outcomes does not apply to these endpoints.

The 80% power column means the number of participants per arm in a hypothetical study that would have an 80% chance of detecting the specified effect at the stated significance level, if the calculation assumptions and effect were correct. The 90% power column expresses the corresponding planning target for a 90% chance. Neither column describes the power achieved by the completed trial. These figures are not observed power.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. The figures therefore rise as the assumed effect moves from 100% to 75% and then 50% of the observed effect. The observed effect itself is uncertain, particularly because the primary confidence interval is broad and includes zero. A planning illustration based on an observed estimate should not be mistaken for a reliable forecast of the sample size needed to detect a true effect.

The original trial’s own sample-size justification and design assumptions are not reported in the registry record. The listed calculations are separate planning illustrations, not evidence about the reasoning behind the enrollment of 82 participants. They do not establish whether the original trial was adequately sized for its prespecified objective, which is not reported in the registry record.

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 = 0.575; treatment proportion p₁ = 0.476; average p̄ = 0.526.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7062 = 1.3841.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7027 = 0.5914.
4. n = (1.3841 + 0.5914)² / (-0.0988)² = 399.7, rounded up to 400 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 <- 0.575                          # control proportion
p1 <- 0.476190476190476                          # 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(1658995)
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 = 400 (80% power), 535 (90% power)
 75% of observed effect: n per arm = 710 (80% power), 950 (90% power)
 50% of observed effect: n per arm = 1,591 (80% power), 2,129 (90% power)
power.prop.test: 399.7 
Simulated power at n = 400 per arm: 0.802 (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 sponsor-reported primary analysis is a Chi-squared comparison of risk difference. It reports a risk difference of -9.9, a 95% confidence interval from -31.4 to 11.6, and p = 0.37. The independent recalculation from the posted counts gives a risk difference of -0.099, a 95% confidence interval from -0.314 to 0.116, and an unadjusted p-value of 0.37. The estimates agree closely once the different scales used for the risk difference are recognized.

Because the recalculation is a simple unadjusted reconstruction, it is useful as a check on the summary counts, not as a replacement for the sponsor’s own analysis. In this case, the registry results do not indicate a discrepancy between the sponsor-reported primary result and the recalculated result. The sponsor’s analysis remains the reported analysis to use when describing the trial’s primary finding.

The registry also reports a Chi-squared p-value of 0.46 for subject satisfaction, without a reported effect estimate or confidence interval for that analysis. The recalculated satisfaction comparison is not a substitute for a missing sponsor-reported interval. No sponsor analysis is posted for implant removal. The absence of a reported analysis should not be filled in by treating a recalculation as if it were the trial’s prespecified analysis.

The record does not report whether the sponsor used additional adjustments or analysis-population rules beyond the information attached to the posted result. For the primary outcome, no numerical conflict is apparent in the reported and recalculated summaries. For other outcomes, differences in what is reported mean that the sponsor analysis and the recalculations have different levels of available detail.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and two secondary outcomes, but it does not report a multiplicity adjustment, testing hierarchy, or other strategy for controlling the interpretation of multiple comparisons. In general, testing several outcomes can increase the chance that at least one result appears statistically notable by chance. A prespecified approach can help distinguish a primary confirmatory result from secondary or exploratory findings. Without a reported plan, secondary p-values should be interpreted cautiously and should not be treated as independent confirmations of the primary result.

The trial record also does not report the original statistical analysis plan, the definition of the analysis population, or the handling of missing observations. These omissions are relevant because the outcome denominators differ: the primary endpoint and removal outcome use 42 and 40 participants, while satisfaction uses 34 and 33. The record does not explain the difference in satisfaction denominators, describe reasons for missing data, or state whether any imputation or sensitivity analysis was used. It is therefore not possible to determine from the registry record whether those participants were unavailable, excluded under a rule, or handled another way.

The registry does not describe whether the analyses followed an intention-to-treat principle, a per-protocol approach, or another population definition. It also does not report how outcome requests were adjudicated, whether all randomized participants were followed through the stated timeframes, or whether any interim analyses occurred. These matters should not be guessed from the reported counts.

These reporting gaps do not invalidate the posted results, but they limit assessment of robustness and completeness. They also make it difficult to determine whether the analyses were fully aligned with the original plan. The primary comparison can still be described as posted, with its reported estimate, interval, and p-value; stronger claims about the analysis strategy or the treatment of missing data are not supported by the registry record.

16. 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 0% reporting threshold.

The adverse-event figures report zero serious adverse events in the doxycycline group among 42 participants at risk and zero in the placebo group among 40 participants at risk. The record also reports zero other adverse events in each group and zero deaths in either group. No serious adverse-event terms are listed.

These are the posted counts for the trial record. They indicate that no events in those categories were recorded in the reported safety results; they do not establish that no adverse events could occur, or provide a precise estimate of the frequency of uncommon events. The registry does not provide further detail about safety definitions, event collection procedures, severity grading, or the duration of safety surveillance. It also does not report a separate statistical comparison of safety outcomes.

Safety counts should be read separately from the efficacy outcome. The absence of reported events in these categories does not change the uncertainty in the primary outcome, and it should not be interpreted as a general conclusion about safety beyond the participants and reporting captured in this record.

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

The posted primary result describes the difference between randomized groups in the proportion requesting additional treatment after the initial course. The sponsor-reported estimate is -9.9, with a 95% confidence interval from -31.4 to 11.6 and p = 0.37. The interval includes no difference and values on either side of it. These data therefore do not establish a clear difference between doxycycline and placebo on the registry-defined primary outcome.

That interpretation is narrower than saying the treatments are the same. A nonsignificant result does not prove equivalence, and no equivalence margin is reported. The confidence interval leaves room for more than one possible underlying difference. The trial’s enrollment of 82 and the endpoint counts do not support certainty about small or moderate differences solely from the point estimate.

The endpoint is a request for additional treatment, not a direct measurement of bleeding severity or duration. A request can be relevant to treatment experience, but the registry does not report the reasons for requests or link each request to a standardized symptom assessment. The primary result cannot answer questions about outcomes that were not reported, including detailed bleeding patterns, longer-term outcomes beyond the stated timeframe, or subgroup effects.

The satisfaction and implant-removal outcomes add separate information but are secondary and remain uncertain. Their findings do not establish a clear difference, and the record does not report a multiplicity plan or a complete analysis plan. The safety record reports zero serious and other adverse events in both groups and zero deaths, but it does not establish that uncommon events are absent.

In general, a trial result is best interpreted by considering the outcome definition, the estimate, its precision, the design, and the completeness of reporting. For this trial, the central statistical message is uncertainty around the primary between-group contrast. The posted result supports describing what was observed in these groups, but not a broader claim about all users of the implant, all bleeding outcomes, or effects not assessed in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and its uncertainty should be read together. The primary estimate is negative, but its 95% confidence interval spans zero and extends to values favoring either group. Looking only at the point estimate would hide how much uncertainty remains; looking only at whether the p-value is below a threshold would also omit the range of compatible contrasts.

It also shows the value of naming the outcome precisely. A request for subsequent treatment is a concrete participant-level event, but it is not the same as symptom severity, bleeding duration, satisfaction, or removal of the implant. Those related outcomes can tell different parts of the story. Clear distinctions help prevent a result for one measure from being generalized to outcomes it did not assess.

The record supports comparing the sponsor’s primary result with a straightforward calculation from the posted counts. Their close agreement is reassuring as a consistency check, while the sponsor analysis remains the primary reported analysis. At the same time, secondary outcome reporting is less complete: one sponsor-reported analysis gives only a p-value, and no sponsor analysis is posted for implant removal. That contrast highlights the importance of complete estimates and intervals across outcomes.

Finally, the record leaves important methodological details unreported, including the original sample-size justification, missing-data handling, analysis populations, and multiplicity strategy. These omissions limit the strength of interpretation even when the posted numbers are clear. Statistical reading is not only a matter of calculating contrasts; it also requires attention to what was measured, how completely it was reported, and what remains unknown.

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 has limited detail about the enrolled population beyond the condition and the description of dissatisfaction with bleeding after 13 weeks post-implant insertion. Baseline characteristics, eligibility criteria, and subgroup definitions are not reported in the registry record. This restricts assessment of how representative the participants were and whether outcomes differed across participant characteristics.

The primary endpoint records requests for additional treatment. The record does not describe the reasons for requests, a standardized bleeding assessment, or the criteria used to classify an event. This means the endpoint should not be treated as a direct measurement of symptom severity. The follow-up windows also differ among outcomes: primary requests are tracked after initial treatment up to 39 weeks, satisfaction is assessed at 13 weeks post-treatment, and removal is assessed at 26 weeks post-randomization.

Outcome denominators differ for satisfaction, and the registry does not explain why or how missing observations were handled. The record does not report an analysis-population definition, an intention-to-treat designation, or sensitivity analyses. It also does not report the original sample-size justification, the prespecified statistical plan, or a multiplicity approach. These gaps limit evaluation of the completeness and robustness of the reported analyses.

The registry’s masking descriptions differ: the structured record identifies triple masking, while the brief summary calls the study double-blinded. The record does not clarify which roles were masked. Detailed allocation procedures and procedures for protecting masking are also not reported in the registry record.

Finally, the primary confidence interval is broad and includes no difference. The enrollment and event counts provide limited precision, and the registry does not report a clinically important difference to guide interpretation. These limitations do not change the posted results, but they constrain how confidently those results can be extended beyond the defined endpoints and trial participants.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Management of Etonogestrel Subdermal Implant-related Bleeding — NCT01658995.
• Registry record last updated 2021-01-26; status last verified 2021-01.
• Results first posted 2021-01-26.
• 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

NCT01658995 is a completed, randomized, placebo-controlled, parallel-group Phase 3 trial with 82 enrolled participants. It evaluated a 10-day course of doxycycline against placebo for bleeding associated with an etonogestrel subdermal implant. The registry-designated primary outcome was the number of participants requesting additional secondary treatment after the initial intervention, assessed after initial treatment up to 39 weeks.

The sponsor-reported primary risk difference was -9.9, with a 95% confidence interval from -31.4 to 11.6 and p = 0.37. The interval includes no difference and values in either direction, so the posted result does not establish a clear between-group difference for this outcome. Secondary outcomes were satisfaction and implant removal, with less complete sponsor analysis reporting.

The registry reports zero serious adverse events, zero other adverse events, and zero deaths in both groups. Details about missing-data handling, analysis populations, multiplicity, and the trial’s original sample-size justification are not reported in the registry record.