Progesterone & Postpartum Relapse to Smoking: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Progesterone & Postpartum Relapse to Smoking (NCT01798394), a randomized na study. The primary outcome is Number of Participants Who Relapsed by Week 4 Postpartum.

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, parallel study sponsored by the University of Minnesota. The registry lists the phase as NA and the status as completed. Enrollment was 46. The study start is recorded as 2014-06, and primary completion as 2015-06. The posted arm sizes are 24 for progesterone and 22 for placebo. Those are the reported group sizes; the record does not describe the randomization sequence, allocation concealment, or whether the planned allocation ratio differed from the final group sizes.

The progesterone regimen was a micronized natural progesterone capsule by mouth twice daily, approximately at 8 am and 8 pm, for four weeks beginning on postpartum day 4. The placebo regimen used a capsule on the same schedule and for the same duration. The project summary also refers to supplemental relapse prevention counseling and feasibility work on enhanced compliance monitoring and identification of factors affecting outcomes. Further operational details about counseling and monitoring are not reported in the registry record.

The primary outcome was the number of participants who relapsed by week 4 postpartum. The registry lists secondary outcomes on relapse by week 12, relapse at any time during postpartum up to Day 84, visits attended, compliance determinants, doses taken, and electronic data capture forms completed. Results are posted for the first three secondary outcomes, but not for every listed secondary outcome. The registry record does not report the original sample-size justification, planned statistical analysis, or a detailed analysis population. The recorded enrollment and arm sizes therefore describe the trial record, not the adequacy of its original design.

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 Number of Participants Who Relapsed by Week 4 Postpartum, measured over Week 4 Postpartum.

The primary endpoint is the number of participants who relapsed by week 4 postpartum. Its definition is based on seven-day point prevalence: a participant meets the relapse definition if there was a single puff of a cigarette during the seven days before a prespecified time point. The endpoint is binary at the participant level: each participant either met the stated definition at the assessment or did not. The posted result gives counts for each arm rather than a continuous measure of smoking intensity.

A short, prespecified recall window makes the endpoint a direct way to record whether smoking occurred near the assessment time. The same definition can be applied in both arms, allowing the observed counts and risks to be compared. It also has limitations: it does not describe the timing or frequency of smoking outside that recall window, and a result at the assessment does not by itself describe the full postpartum course. The registry record does not report the procedures used to verify smoking status or the handling of missing endpoint assessments.

The stated time point matters to interpretation. The primary outcome concerns relapse by week 4 postpartum, while separate secondary outcomes address later postpartum time frames. Those outcomes are related but are not interchangeable: each has its own assessment window and can reflect a different portion of the postpartum experience.

7. Results Posted in the Registry

• Progesterone: 25.0% (6/24) versus 31.8% (7/22) on control; risk difference -6.8 percentage points (95% CI -32.9 to 19.2), risk ratio 0.79 (0.31–1.98); unadjusted two-proportion z-test p = 0.608.

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.

Number of Participants Who Relapsed by Week 12 Postpartum

• 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:
  • Progesterone: 45.8% (11/24) versus 59.1% (13/22) on control; risk difference -13.3 percentage points (95% CI -41.9 to 15.4), risk ratio 0.78 (0.44–1.35); unadjusted two-proportion z-test p = 0.369.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Progesterone and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Relapsed at All During Postpartum (up to Day 84)

• 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:
  • Progesterone: 41.7% (10/24) versus 59.1% (13/22) on control; risk difference -17.4 percentage points (95% CI -45.9 to 11.1), risk ratio 0.71 (0.39–1.27); unadjusted two-proportion z-test p = 0.238.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Progesterone and the control. The interval gives the range of effects that remain compatible with the data.

Protocol Compliance - Number of Visits Attended

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Progesterone: mean 4.50 versus 4.40 on control; difference 0.10 (95% CI -0.57 to 0.77), standardized effect d = 0.09; z-test p = 0.769.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Progesterone and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results follow a broadly consistent direction for the relapse outcomes: the point estimates favor the progesterone arm, while the visit-attendance means are close. The relapse comparisons concern later or broader postpartum windows than the primary week 4 assessment, so they provide related but distinct views of outcome over time. They do not replace the primary endpoint or make its uncertainty disappear. Their confidence intervals also extend across no difference, so the secondary relapse results do not resolve whether the underlying risks differ.

Across these outcomes, the pattern is compatible with the direction of the primary point estimate, but the estimates remain uncertain. Repeatedly observing estimates in a similar direction can be descriptively informative, yet related endpoints measured in the same trial are not independent confirmations. The same participants and study conditions contribute to multiple comparisons, and differences in outcome windows can affect the results.

The registry lists additional compliance outcomes, including compliance determinants, medication doses taken, and electronic data capture forms completed, but does not post results for all of them. The number of visits attended is reported, while details for the other listed outcomes are not reported in the registry record. The secondary analysis results are not listed in a sponsor-reported analysis set.

Unadjusted secondary results carry less weight because multiple outcomes and time points create more opportunities for apparently notable findings by chance. The registry record does not report a multiplicity strategy, a hierarchy of secondary hypotheses, or adjusted analyses. These results are best treated as supportive or exploratory descriptions rather than as standalone confirmatory evidence. They add context about the observed pattern, but do not establish a treatment effect or compensate for the imprecision of the primary result.

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

• Number of Participants Who Relapsed by Week 12 Postpartum
• Number of Participants Who Relapsed at All During Postpartum (up to Day 84)
• Protocol Compliance - Number of Visits Attended
• Compliance Determinants
• Protocol Compliance - Doses of Medication Taken
• Protocol Compliance - EDC's Completed

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary, because the registry defines relapse as either present or absent at the specified assessment. For each arm, the posted count can be interpreted alongside its arm size to describe the observed risk. Comparing risks makes clear that the endpoint is about the proportion of participants meeting the relapse definition, rather than the number of cigarettes smoked or a rate of smoking over time. The posted comparison reports an unadjusted risk difference and also gives relative measures.

What does the risk difference describe?

A risk difference subtracts the comparator-arm risk from the intervention-arm risk. With progesterone as the intervention and placebo as the comparator, a negative difference means the recorded risk was lower in the progesterone arm; a positive difference means it was higher. The estimate is -0.068. Its interval runs from -0.329 to 0.192, so it includes zero. Zero represents no difference in the measured risks. Because the interval extends to either side of zero, it is consistent with a range that includes a lower risk, no difference, and a higher risk in the progesterone arm. The interval's confidence level is not reported in the registry record.

How do relative measures differ?

The risk ratio compares the risk in the progesterone arm with the risk in the placebo arm by division. A ratio of 1 represents equal risks; values below 1 indicate a lower risk in the intervention arm, and values above 1 indicate a higher risk. The posted risk ratio is 0.786, with an interval from 0.312 to 1.98. The odds ratio compares odds rather than risks. Its posted estimate is 0.714, with an interval from 0.197 to 2.589. The odds ratio and risk ratio can differ in magnitude because they are different measures, and neither should be mistaken for an absolute difference in risk. Their intervals both include the value corresponding to no relative difference.

What does the p-value contribute?

The unadjusted p-value is 0.608. In general, a p-value describes how unusual the observed data, or data more extreme, would be under a stated null model and its assumptions. It does not give the probability that the null is true, measure the probability that a treatment effect is real, or quantify the clinical importance of the observed difference. It should be read together with the estimated effect and its interval. The registry does not report a multiplicity-adjusted p-value or a detailed test specification for this comparison. No sponsor-reported analysis is listed.

Why does the binary outcome matter?

Binary outcomes discard some information about the amount and pattern of smoking. A participant who meets the single-puff definition and a participant with more frequent smoking both count as relapse under the posted definition. That rule can make the outcome clear and consistently classifiable, but it cannot represent the full variation in smoking behavior. A seven-day point-prevalence assessment also describes a particular recall window; it is not the same as continuous monitoring across the postpartum period. The registry record does not report additional verification procedures.

Randomization can support a comparison of assigned groups when it is implemented as planned and when outcome measurement and follow-up are appropriately handled. The registry identifies the trial as randomized and double-masked, but it does not report enough procedural detail to evaluate sequence generation, concealment, adherence to masking, or all aspects of follow-up. The posted endpoint counts are therefore informative descriptive results, while a fuller causal interpretation requires information not reported in the registry record.

Finally, the posted comparisons are unadjusted. Adjustment can be used in some analyses to account for prespecified covariates or design features, but the registry record does not provide an analysis plan explaining whether or how that was intended. No adjustment should be assumed. General statistical interpretation also depends on whether participants with missing assessments were excluded, counted in another way, or handled through a model; that approach is not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the possible size of an effect. For the primary risk difference, the point estimate is -0.068 and the interval extends from -0.329 to 0.192. That range is broad relative to the point estimate and includes zero. It also allows for differences in either direction. The result therefore does not pin down the size or direction of the underlying risk difference with high precision. The confidence level for the posted interval is not reported in the registry record.

The relative estimates are similarly uncertain. The risk-ratio interval, from 0.312 to 1.98, includes the no-difference value of 1 and spans values on either side. The odds-ratio interval, from 0.197 to 2.589, also includes 1. These intervals indicate that the observed data are compatible with materially different relative comparisons. The point estimates alone should not be treated as definitive descriptions of the underlying effect.

In general, a confidence interval gives a range of estimates compatible with the data and the method used to construct it; it communicates uncertainty more directly than a point estimate alone. Its interpretation depends on the interval method, assumptions, and confidence level. Those details are not reported in the registry record. The group sizes and number of observed relapses are modest, and sparse binary outcome data can produce substantial uncertainty. That general feature helps explain why a small-looking difference in the observed counts does not yield a narrow estimate.

Intervals that include no difference do not prove that there is no effect, and they do not demonstrate equivalence. Conversely, an interval that permits a lower risk does not establish that a lower risk is the true result. The practical meaning depends on which effects would matter for the research question, but a threshold for meaningful benefit or harm is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrative sample sizes per arm for a future study, not totals across arms and not observed trial results. They are based on the observed effect in this trial and use a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. Each scenario sets the effect to detect as a stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

For each effect scenario, the 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting that assumed effect under the stated planning assumptions, if the effect is present. The 90% power column expresses the corresponding planning target for a 90% chance. These are design targets, not guarantees, and they depend on the assumptions used in the calculation. They do not describe the power achieved by the completed trial.

Smaller effects require more participants to detect reliably, which is why the planning figures increase as the assumed effect is reduced from 100% to 75% to 50% of the observed effect. The primary endpoint's planning figures are 686 and 918 participants per arm for the 100% scenario, 1,242 and 1,662 for the 75% scenario, and 2,842 and 3,804 for the 50% scenario, for 80% and 90% power respectively. These illustrations use the observed risk difference as their starting point; they do not establish that the same effect would recur in another study. This is not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.318; treatment proportion p₁ = 0.250; average p̄ = 0.284.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6378 = 1.2500.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6360 = 0.5352.
4. n = (1.2500 + 0.5352)² / (-0.0682)² = 685.6, rounded up to 686 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 <- 0.318181818181818                          # control proportion
p1 <- 0.25                          # 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(1798394)
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 = 686 (80% power), 918 (90% power)
 75% of observed effect: n per arm = 1,242 (80% power), 1,662 (90% power)
 50% of observed effect: n per arm = 2,842 (80% power), 3,804 (90% power)
power.prop.test: 685.6 
Simulated power at n = 686 per arm: 0.796 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes in addition to the primary relapse endpoint. Testing or interpreting multiple outcomes increases the chance that at least one result may appear noteworthy even when there is no corresponding underlying effect. A prespecified hierarchy, correction procedure, or clear distinction between confirmatory and exploratory outcomes can help readers understand how to interpret a collection of results. Such a multiplicity plan is not reported in the registry record. The posted comparisons are unadjusted, and no multiplicity-adjusted results are listed.

Missing-data handling is another important part of interpreting the endpoint counts. The record reports the arm sizes and event counts, but does not explain whether every randomized participant had an observed primary assessment, how missing assessments were handled, or whether any participants were excluded from the analysis. It also does not report imputation methods or sensitivity analyses for missing outcomes. The arm sizes should not be assumed to define the analysis population without that information.

The record identifies the trial as randomized, but the intended analysis population—such as all randomized participants or a defined subset—is not reported in the registry record. A detailed statistical analysis plan, model specification, covariate adjustment plan, and analysis timing are also not reported. The number of reported analyses is recorded as 0, and no secondary reported analyses are listed. This absence does not establish what analyses were conducted outside the posted registry information.

These gaps limit assessment of whether the reported comparisons follow a prespecified plan and how sensitive the findings may be to analysis choices. They do not invalidate the descriptive counts, but they mean that the posted summaries alone cannot answer questions about missingness, selective reporting, or robustness across analysis populations. Readers should therefore distinguish the observed arm summaries from a complete account of the trial's statistical conduct.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: hospitalization for post-cesarean section infection (4.5%).

The registry records serious adverse events among 24 participants at risk in the progesterone arm and 22 at risk in the placebo arm. It reports 0 serious adverse events for progesterone and 1 for placebo. Other adverse events are recorded as 0 in each arm. These figures describe the safety information posted in the registry; they do not by themselves establish whether an event was caused by the assigned treatment.

The serious-event term listed is hospitalization for post-cesarean section infection, with 4.5% shown. The record does not identify the arm associated with that term in the posted term summary, so it should not be attributed to either arm based on these details. The deaths fields are not populated with a count; deaths are not reported in the registry record. The registry does not provide further detail about event timing, severity grading, relatedness assessments, or the duration and completeness of adverse-event surveillance. These figures should be read as the posted event record, not as a comprehensive comparison of all possible safety outcomes.

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

The results describe a small randomized comparison of progesterone and placebo in a postpartum smoking-relapse study. At the primary week 4 assessment, the observed relapse risk was lower in the progesterone arm than in the placebo arm, but the estimated risk difference is imprecise. Its interval includes no difference and extends in both directions. The unadjusted p-value likewise does not provide evidence that clearly separates the observed comparison from no difference under its analysis assumptions.

This does not mean that the arms are equivalent. Demonstrating equivalence would require an appropriate design, a prespecified equivalence margin, and an analysis suited to that question; such details are not reported in the registry record. It also does not mean that the intervention has no effect. The available estimate remains compatible with more than one underlying effect, and the posted data do not resolve which is most plausible.

The result is specific to the registry's relapse definition and assessment window. It concerns a single puff during the seven days before a specified time point by week 4 postpartum. It does not directly measure long-term smoking status, smoking frequency, or all relapse experiences throughout postpartum. The secondary outcomes address other postpartum windows, but their unadjusted and imprecise results do not establish a different conclusion.

Interpretation also depends on information that is not reported in the registry record, including detailed eligibility criteria, outcome verification, missing-data handling, the analysis population, the original analysis plan, and multiplicity procedures. Therefore, the most appropriate conclusion is descriptive: the recorded groups had the posted outcomes, and the estimated primary difference favors progesterone in direction but is too imprecise to establish the size or direction of an underlying difference. The statistics do not warrant medical advice or a treatment recommendation.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its point estimate and uncertainty tell different parts of the story. The primary estimate is in the direction of lower observed relapse risk with progesterone, yet its interval is broad and crosses the no-difference value. Reporting only the point estimate would overstate certainty; reporting only the unadjusted p-value would obscure the range of effects compatible with the data. Reading both with the arm counts gives a more complete account.

The study also illustrates how outcome definitions shape conclusions. A binary seven-day point-prevalence relapse measure is clear to interpret, but it compresses smoking behavior into whether the threshold was met at a particular assessment. It cannot describe the amount or continuity of smoking. The later relapse outcomes use different windows, making it important to keep their meanings distinct rather than treating them as repeated measurements of an identical endpoint.

Finally, the planning illustrations show why the observed effect should not be treated as a reliable forecast for a future study. Sample-size requirements rise as the assumed target effect becomes smaller. Because the trial's estimate is imprecise, planning directly from that observed effect is only an illustration, not a design justification. The registry also lacks the original sample-size rationale and detailed analysis plan. Together, these features emphasize the value of clear endpoint definitions, transparent analysis plans, careful reporting of uncertainty, and restraint when interpreting multiple outcomes from a modest study.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The main trial-specific limitation in interpreting these results is the limited amount of outcome information: the posted primary comparison includes 6 relapses among 24 participants in the progesterone arm and 7 among 22 in the placebo arm. The resulting interval is wide, so the estimated difference is not precise. The registry record does not report a prespecified threshold for a clinically meaningful difference, which further limits judgments about practical importance.

The registry does not report detailed eligibility criteria, the characteristics of participants at baseline, or the smoking status required for enrollment. This makes it difficult to judge how closely the enrolled group represents other postpartum populations or to assess the balance of prognostic characteristics between arms. Randomization is recorded, but sequence generation and allocation concealment details are not reported.

The endpoint relies on a seven-day point-prevalence definition and the record does not describe biochemical verification or other procedures for confirming self-reported smoking. Missing-assessment handling and the analysis population are also not reported. Without these details, it is difficult to evaluate possible measurement or attrition effects. The registry does not provide a complete outcome set for all listed compliance measures, and it does not report multiplicity procedures or a detailed statistical analysis plan.

These limitations do not erase the posted observations, but they constrain the strength and scope of interpretation. The results apply to the recorded endpoint and study context; they should not be generalized beyond that evidence without additional information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Progesterone & Postpartum Relapse to Smoking — NCT01798394.
• Registry record last updated 2017-01-09; status last verified 2016-11.
• Results first posted 2017-01-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The completed, randomized, double-masked, parallel trial compared progesterone with placebo for postpartum smoking relapse. The registry reports enrollment of 46 and arm sizes of 24 for progesterone and 22 for placebo. The primary endpoint was relapse by week 4 postpartum, defined as a single puff during the seven days before a prespecified assessment. The observed counts were 6 and 7, respectively. The estimated risk difference was -0.068, with an interval from -0.329 to 0.192 and an unadjusted p-value of 0.608.

The point estimate favors progesterone, but the interval includes no difference and allows effects in either direction. Posted secondary relapse estimates point in a similar direction but remain uncertain; visit attendance was similar. The registry does not report a detailed analysis plan, missing-data approach, multiplicity strategy, or original sample-size justification. Planning figures are illustrations based on the observed effect, not observed trial power. Safety records list 0 serious adverse events for progesterone and 1 for placebo, with further event details limited in the registry.