Estrogen Variability and Irritability During the Menopause Transition: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Estrogen Variability and Irritability During the Menopause Transition (NCT05388656), a randomized phase 4 study. The primary outcome is Mean IDAS Ill Temper Scale Score Over Time.

2. Clinical Question

3. Trial Design

This is a Phase 4, randomized, quadruple-masked, crossover trial sponsored by the University of North Carolina, Chapel Hill. The registry lists an enrollment of 40 and a completed status. The study began on 2022-06-15, and primary completion was recorded as 2024-12-17. Those record dates describe the trial timeline; they do not give the dates when individual participants entered or completed treatment.

The principal comparison is between estradiol and placebo. The registry describes two sequences: estradiol followed by placebo, and placebo followed by estradiol. Each treatment period is described as lasting 3 weeks, with a washout period of 3 weeks between the two periods. Because this is a crossover design, the treatment order is part of the study structure: each sequence places the active and placebo periods in a different order. The registry does not report further details about sequence generation, adherence, or how the washout was selected.

Quadruple masking indicates that the record classifies the trial as masked at four levels, but the specific roles masked are not reported in the registry record. The overall enrolled number and the outcome-specific numbers are not identical in the posted summaries: the primary outcome lists 33 participants for estradiol and 31 for placebo. These are the counts shown for the outcome and should not be mistaken for the enrollment total or interpreted as an explanation of missing observations.

Progesterone 200 mg is listed among the interventions, and safety results include a progesterone group. However, the available arm descriptions focus on the estradiol/placebo sequences and end before fully describing what happened after the second intervention. The registry record does not report enough detail to reconstruct the progesterone regimen or its relation to the primary efficacy comparison.

4. Participant Flow and Accounting

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

Before assignment: Forty participants signed informed consent and were enrolled into the study. Of the 40 enrolled participants, 34 met eligibility criteria and proceeded directly to study assignment. Participants who were excluded prior to assignment were those who did not complete initial eligibility confirmation or withdrew consent.

First Intervention (3 Weeks)

Washout (3 Weeks)

Second Intervention (3 Weeks)

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 Mean IDAS Ill Temper Scale Score Over Time, measured over 3 weeks during each intervention.

The primary endpoint is mean IDAS Ill Temper Scale score over time, assessed during the 3 weeks of each intervention. The registry describes the scale as five symptom items, each rated from 1, not at all, to 5, extremely. The total score may range from 5-25, with higher scores indicating more severe irritability. Daily irritability scores are averaged for each treatment condition, so the posted outcome summarizes symptom severity across the intervention period rather than reporting a single-day score.

Irritability is used because the registry describes it as a prominent source of affective impairment and distress among perimenopausal women with affective impairment. The study’s stated purpose is to investigate susceptibility to estradiol fluctuation and irritability symptoms. This makes the symptom scale a direct measure of the clinical experience the primary comparison is intended to examine, while the secondary measures address neurophysiological responses.

A mean is a useful summary for a continuous score, but it does not show how individual participants’ scores were distributed or how their symptoms changed day to day. The standard deviation gives information about variability among the observations summarized for each condition. Neither summary alone describes the full repeated-measures pattern. The registry record does not report a more detailed definition of the primary analysis population or the treatment of incomplete daily ratings.

7. Results Posted in the Registry

• Estradiol: mean 6.19 versus 6.02 on control; difference 0.17 (95% CI -0.41 to 0.75), standardized effect d = 0.14; z-test p = 0.565.

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.

Reward Positivity (RewP) in Response to the Affective Posner Paradigm

• 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:
  • Estradiol: mean -2.59 versus -2.13 on control; difference -0.46 (95% CI -2.01 to 1.09), standardized effect d = -0.15; z-test p = 0.560.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Estradiol and the control. The interval gives the range of effects that remain compatible with the data.

Mean LPP Amplitude During Implicit Viewing Task Dysfunctional Threat Processing Was Indexed by Greater Late Positive Potential (LPP) Component for Emotional Face Stimuli, Elicited 400-900 Milliseconds After the Stimulus Presentation.

• 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:
  • Estradiol: mean 2.92 versus 2.99 on control; difference -0.07 (95% CI -0.83 to 0.69), standardized effect d = -0.04; z-test p = 0.857.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Estradiol and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the study’s focus from reported irritability to neurophysiological measures: reward positivity in response to the Affective Posner Paradigm, and late positive potential during an implicit viewing task involving emotional face stimuli. The registry reports a mixed-model analysis for each. The tables and plots give the outcome-specific summaries; this discussion considers their overall place in the evidence rather than restating each result.

Across the secondary endpoints, the posted model-based analyses suggest stronger statistical evidence than the simple unadjusted recalculations. The recalculated comparisons have confidence intervals that include zero, while the registry’s model-based p-values are smaller. As with the primary endpoint, the record does not include model estimates and intervals that would allow a direct comparison of effect size and precision across the approaches. A difference in significance indicators does not resolve the underlying uncertainty or identify the model details responsible.

The secondary outcomes do not change the primary endpoint’s interpretation. They measure different constructs and are not substitutes for the IDAS irritability score. Their results may be relevant to the study’s stated interest in neurophysiological mechanisms, but the registry record does not establish a mechanism from these summaries. The primary result remains the central symptom comparison, and the secondary findings should be considered alongside—not instead of—that result.

Unadjusted secondary results carry less weight when several outcomes are examined because the chance of finding at least one apparently notable result can increase with repeated testing. General statistical explanation: multiplicity procedures can control or otherwise address this issue, but the registry does not report whether an adjustment was planned or applied. Without that information, the secondary p-values should be treated as exploratory signals rather than as stand-alone confirmatory evidence. The record also does not report a hierarchy or prespecified testing order for these outcomes.

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

• Reward Positivity (RewP) in Response to the Affective Posner Paradigm
• Mean LPP Amplitude During Implicit Viewing Task Dysfunctional Threat Processing Was Indexed by Greater Late Positive Potential (LPP) Component for Emotional Face Stimuli, Elicited 400-900 Milliseconds After the Stimulus Presentation.

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the primary measure as a continuous outcome summarized by a mean and standard deviation. This discussion explains the statistical ideas used to read those summaries. General explanations are identified as such; details of the trial’s exact model are limited to what the registry reports.

What does a mean difference describe?

A mean difference compares the average outcome in one condition with the average in another. Here the posted comparison is estradiol versus placebo for the IDAS Ill Temper Scale. A positive difference means the estradiol mean is higher than the placebo mean under the subtraction order used in the comparison; it does not by itself tell whether the difference is clinically important. Clinical importance requires a meaningful threshold or context, and such a threshold is not reported in the registry record.

The arm means and standard deviations are summaries of observations, not a display of each participant’s path through both treatment periods. A mean can conceal variation in individual responses, and a standard deviation describes spread rather than uncertainty in the estimated mean. The standard errors shown in the calculated output reflect uncertainty for the individual condition means under that calculation. They do not recover the participant-level correlation inherent in a crossover study.

Why does the crossover structure matter?

General statistical explanation: a crossover design observes participants in more than one treatment condition, so each participant may contribute information under both conditions. A paired analysis can compare each participant with themself and account for the association between their repeated measurements. This can affect the estimated uncertainty. A comparison based only on separate means and standard deviations treats the condition summaries as if the pairing information were unavailable. In this trial, the published summary statistics do not include the within-participant covariance, so a paired estimate cannot be reconstructed from the displayed arm summaries alone.

The record describes treatment order and a washout, but it does not report whether or how the analysis assessed period effects, sequence effects, carryover, or incomplete crossover participation. These are design and analysis considerations in crossover studies, not findings that can be inferred from the posted means. The reported method is called Mixed Models Analysis; the registry does not describe its fixed effects, random effects, covariance structure, or handling of missing measurements.

What does a mixed model generally do?

General statistical explanation: a mixed model can represent both systematic features of the study, such as treatment or period, and participant-level variation. It can be useful when observations are repeated or clustered, because observations from one person are not necessarily independent. The model’s validity depends on how it is specified and on the assumptions made about the data. The label Mixed Models Analysis alone does not reveal which terms were included or how the model treated incomplete records.

The registry reports a model-based p-value for each outcome, but does not report a corresponding estimate or confidence interval. Without those details, readers cannot evaluate the size and precision of the model-based treatment contrast from the registry record alone. A p-value does not communicate the direction or magnitude of an effect; it summarizes how compatible the observed data are with a particular null hypothesis under the method’s assumptions.

How should the unadjusted recalculation be understood?

The calculated comparison uses the posted condition means, standard deviations, and sample sizes to produce a simple unadjusted difference, confidence interval, and p-value. It does not adjust for covariates, model the crossover sequence, or reproduce the registry’s mixed-model analysis. It is therefore a check on the posted summary statistics, not a replacement for the trial’s reported analysis. The record’s discrepancy indicator is false, but this does not mean that every method yields the same result; the displayed model and simple recalculation are different approaches.

General statistical explanation: a p-value is not the probability that a treatment effect is absent, nor is it a measure of effect size. A confidence interval gives a range of estimates compatible with the data and the method, and its width helps communicate precision. If an interval includes zero for a mean difference, the data are compatible with no difference under that calculation, as well as with values on either side of zero within the interval. This should not be translated into proof of equivalence.

Why consider variability?

General statistical explanation: variability matters because greater spread makes an estimated mean less precise when other features are held constant. Standard deviations describe observed dispersion, while standard errors describe uncertainty in an estimate. Over-dispersion is most often discussed for count outcomes when observed variability exceeds what a chosen count model expects. The primary endpoint is continuous, and the registry does not report an over-dispersion assessment. There is no basis in the record to claim that over-dispersion was present or that a particular correction was applied.

Finally, the registry does not report a formal sample-size justification, the assumptions behind the original trial design, a detailed missing-data strategy, or a multiplicity plan. These omissions limit independent assessment of the analysis but do not change what the posted descriptive summaries say. The planning illustrations on this page are separate calculations based on observed effects, not a reconstruction of the original protocol.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 0.17. Its confidence interval, as displayed in the results table, extends from a value below zero to a value above zero. This means the interval includes no difference and also includes differences in either direction. The interval is not evidence that the true effect is exactly zero; it shows that the summary data do not pin down a single value with high precision under this unadjusted calculation.

The treatment-period means are close in the posted summary, but the uncertainty interval is more informative than the means alone. It signals that the data are compatible with a range of possible treatment contrasts. The registry does not provide the mixed-model estimate or interval for the primary endpoint, so the precision of the sponsor’s reported model-based contrast cannot be assessed from the posted record.

General statistical explanation: a confidence interval is a method-based range of estimates that reflects sampling uncertainty under the calculation’s assumptions. Its interpretation depends on the model and design information used. In a crossover trial, accounting for within-person association can change the uncertainty compared with a calculation from separate treatment-condition summaries. The recalculated interval does not include participant-level pairing because those data are not posted.

The same caution applies to the secondary outcomes. Their recalculated intervals include zero, while the registry’s mixed-model p-values indicate a different level of statistical evidence. The model estimates and intervals are not reported, limiting direct assessment of their precision. The calculated tables and plots show the numerical intervals; this discussion does not reproduce their endpoints. A reader should distinguish a wide or zero-spanning interval from proof of no effect, and should not treat a small p-value as a substitute for an estimate and its uncertainty.

12. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effect, not a description of the trial’s original design. For these continuous outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrated participants per arm for a design that would have an 80% chance of detecting the assumed effect under those planning assumptions, if that effect and the other assumptions held. The 90% power column uses a higher target chance of detection and therefore shows a larger required number for the same assumed effect. These are prospective planning quantities; they are not the probability that this completed trial detected an effect.

The table shows planning for 100%, 75%, and 50% of the observed effect. As the assumed effect becomes smaller, more participants are needed in each arm to reach the same target power. For the primary endpoint, the displayed planning values range from 770 participants per arm for 80% power at 100% of the observed effect to 4,120 participants per arm for 90% power at 50% of the observed effect. The secondary endpoint tables show the same general relationship, with their own observed effects and corresponding illustrations.

These figures depend heavily on the observed effect, which can be an uncertain basis for planning, especially when the observed estimate is imprecise. The calculations also use equal allocation and a normal approximation; they are not a reconstruction of a crossover-specific design calculation. This is not observed power. Use the table and curve to understand how assumed effect size and target power affect planning, not to judge the trial’s success after the fact.

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

Worked calculation for this trial

1. Observed difference Δ = 0.170; pooled standard deviation σ = 1.190.
2. n = 2 × (1.96 + 0.842)² × 1.190² / 0.170² = 769.4, rounded up to 770 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 <- 0.170000000000001                      # observed difference in means
sigma <- 1.19012604374495                     # 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(5388656)
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 = 770 (80% power), 1,030 (90% power)
 75% of observed effect: n per arm = 1,368 (80% power), 1,832 (90% power)
 50% of observed effect: n per arm = 3,078 (80% power), 4,120 (90% power)
power.t.test: 770.3 
Simulated power at n = 770 per arm: 0.798 (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.

14. Analyses Reported by the Sponsor

The registry reports the primary analysis as Mixed Models Analysis, with p = 0.09. It reports mixed-model analyses for the secondary outcomes as well. The simple unadjusted recalculations on this page use the posted condition-level means, standard deviations, and sample sizes. For the primary comparison, that recalculation gives a mean difference of 0.17 and p = 0.565. These values are not the sponsor’s model estimate and p-value.

The difference in p-values does not, by itself, establish that one analysis is erroneous. The mixed model may incorporate features that a calculation from summary statistics cannot reproduce, particularly the repeated observations in a crossover design. However, the registry does not report the model specification, model estimate, standard error, or confidence interval needed to explain the difference. The unadjusted calculation also lacks the within-participant covariance required to reconstruct a paired contrast.

Accordingly, read the two results as distinct analyses with distinct available information. The sponsor’s reported analysis is the registry’s model-based result; the recalculation is a transparent, simple comparison based on posted summaries. The record does not provide enough detail to determine exactly why their inferential results differ, or to independently verify the mixed-model output. Neither p-value should be interpreted without considering its method and the estimated effect’s precision.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and two posted secondary outcomes. It does not report a multiplicity adjustment, a testing hierarchy, or whether the analyses were intended as confirmatory or exploratory. General statistical explanation: when multiple outcomes are tested, interpreting each unadjusted p-value as if it were the only test can overstate the strength of the combined evidence. This concern is most relevant to the secondary results, which should not be treated as independent confirmation without a reported plan for handling multiple comparisons.

The record also does not report a detailed missing-data strategy. Outcome-specific participant counts are shown, but the registry does not explain why counts differ across conditions or whether missing daily ratings, incomplete treatment periods, or other circumstances account for the available observations. No imputation method, sensitivity analysis, or assumptions about missingness are described in the posted record. The counts alone cannot establish whether missingness affected the estimates.

Analysis populations are not defined in the registry record. It is therefore not possible to determine from the posted information whether the mixed models used all randomized participants, only participants with data in both periods, or another analysis set. Nor does the record describe how participants who did not complete both periods were handled. These details matter because crossover analyses rely on the structure of observations across periods, and an incomplete record can alter which comparisons contribute information.

The registry identifies a mixed-model method but does not report enough detail to evaluate its exact assumptions or reproduce the analysis. The model terms, covariance structure, treatment of period and sequence, and handling of carryover are not reported in the registry record. These are uncertainties about reporting, not evidence that the analysis was improperly conducted. They define what an independent reader can verify from the posted results.

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.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the estradiol group, zero in the placebo group, and zero in the progesterone group. The groups are listed with 33 participants at risk for serious events for estradiol and 31 each for placebo and progesterone. The deaths column is also zero for each group. These are the serious-event figures shown in the record; they should be read as reported counts, not as proof that serious events are impossible or that risk is absent.

Other adverse events are listed for 18 participants in the estradiol group, 16 in the placebo group, and 7 in the progesterone group. Those figures are separate from the serious adverse-event counts. The registry record does not provide event-term detail in the listed serious-event section, and it does not give enough context to assess severity, duration, relationship to treatment, or comparative risk beyond the posted counts.

Because the treatment periods and group structures differ, the adverse-event counts should not be interpreted as a randomized between-treatment risk estimate without further information about the safety analysis and exposure periods. The registry does not report those details in the available record. These descriptive safety figures do not establish causation and do not support advice about treatment decisions.

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

The posted primary summaries show similar average IDAS Ill Temper Scale scores during the estradiol and placebo periods, with an unadjusted mean difference of 0.17 and a confidence interval that includes zero. The registry’s mixed-model analysis reports p = 0.09, but the model estimate and interval are not reported. The available results therefore do not provide a precise, fully reproducible estimate of the model-based treatment contrast.

These findings do not prove that estradiol and placebo have identical effects. A result that is not statistically persuasive under one analysis is not the same as evidence of equivalence. Equivalence would require a defined margin and an analysis designed to evaluate whether plausible effects fall within that margin; such a margin or analysis is not reported in the registry record. Likewise, the posted summaries do not establish a clinically important difference.

The study was designed around a specific population and question: irritability during the menopause transition and possible susceptibility to estradiol fluctuation. The registry summary gives background context about this population, but the posted outcome summaries do not establish why any participant experienced symptoms or whether a neurophysiological pathway caused them. The secondary outcomes measure different phenomena, and their model-based results cannot be translated directly into an effect on irritability.

General statistical explanation: estimates are more informative when considered with their uncertainty, the design, and the analysis assumptions. Here, the crossover structure makes within-person information important, but it is not included in the posted summary statistics. The registry also leaves the model specification, missing-data approach, analysis populations, and multiplicity plan undescribed. Those limits narrow the claims that can be made from the record.

In short, this page describes the observed summaries and reported analyses rather than making a treatment recommendation. It does not show that treatment should be started, stopped, or changed. It does not establish benefit, lack of benefit, safety for an individual, or generalizability beyond the people and conditions represented in the trial record.

18. Why This Trial Matters Statistically

This trial is statistically instructive because the primary question is examined in a randomized crossover design, while the registry presents both a mixed-model analysis and condition-level summary statistics. Those are not interchangeable. The contrast between the reported model result and the simple recalculation illustrates why readers need to know what observations and assumptions underlie an estimate, particularly when participants contribute data under more than one condition.

The study also illustrates the importance of reporting estimates and uncertainty alongside p-values. The primary comparison has a reported mean difference and an interval in the calculated summaries, but the registry’s mixed-model result is presented without its estimate or confidence interval. Without those model outputs, readers cannot assess the magnitude and precision of the sponsor’s analysis from the record alone. Statistical significance labels cannot fill that gap.

Another useful lesson concerns the difference between the observed trial size and planning illustrations. The enrollment and outcome-specific counts describe this study, while the sample-size table asks how many participants per arm might be needed under stated planning assumptions and assumed effects. Those planning values do not reveal the original design rationale and should not be mistaken for evidence about the study’s probability of success.

Finally, the record gives a clinically focused primary measure and neurophysiological secondary measures, but does not report multiplicity handling, analysis populations, or a detailed missing-data plan. That combination makes the study a clear example of how outcome definitions, design structure, and completeness of reporting jointly shape interpretation. The posted results are useful, but the strength of conclusions depends on details not available in the registry record.

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 main trial-specific limitation for independent interpretation is the gap between the crossover design and the summary information available for recalculation. The posted condition-level means and standard deviations do not show each participant’s paired measurements or their within-person association. As a result, the simple recalculation cannot reproduce an analysis that uses the full crossover structure.

The registry reports mixed-model p-values but not the model estimates or confidence intervals. It does not describe the model terms, covariance structure, or treatment of period and sequence. The treatment sequence and washout are described, but assessments of period effects or carryover are not reported in the registry record. These omissions prevent detailed evaluation of the model-based results.

The primary outcome counts differ between the estradiol and placebo summaries, and the record does not explain why. The overall enrollment is also not the same as the outcome-specific counts. Without a reported missing-data approach and analysis population, readers cannot determine how incomplete observations were handled or whether the displayed counts reflect a particular subset of participants.

The two secondary outcomes have reported mixed-model analyses, but the registry does not report a multiplicity plan or testing hierarchy. Their results should therefore be interpreted cautiously. The registry also lists progesterone and reports its safety counts, while the available arm descriptions do not fully explain its role in the intervention sequence. Finally, the record does not report the original sample-size justification, eligibility details, or a clinical threshold for an important change in irritability. These are limits on interpretation, not evidence that the trial was conducted incorrectly.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Estrogen Variability and Irritability During the Menopause Transition — NCT05388656.
• Registry record last updated 2025-11-26; status last verified 2025-06.
• Results first posted 2025-11-26.
• 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

The registry record describes a completed Phase 4, randomized, quadruple-masked crossover trial sponsored by the University of North Carolina, Chapel Hill, with enrollment of 40. It compares estradiol and placebo across intervention periods and identifies mean IDAS Ill Temper Scale score over time as the primary outcome. The posted primary means are 6.19 for estradiol and 6.02 for placebo; the unadjusted recalculation gives a mean difference of 0.17 and p = 0.565. The registry reports a mixed-model primary p-value of 0.09.

Two secondary neurophysiological outcomes are posted, each with a mixed-model analysis. The registry also lists progesterone and reports serious and other adverse-event counts. Model specifications, analysis populations, missing-data methods, multiplicity handling, and the original sample-size justification are not reported in the registry record. The tables, plots, and planning illustrations should be read with those reporting limits in mind.