A Study to Find Out if Fezolinetant Helps Reduce Moderate to Severe Hot Flashes in Women Going Through Menopause - 2: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Find Out if Fezolinetant Helps Reduce Moderate to Severe Hot Flashes in Women Going Through Menopause - 2 (NCT04003142), a randomized phase 3 study. The primary outcome is Change From Baseline in The Mean Frequency of Moderate to Severe VMS at Week 4.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group, placebo-controlled study. The registry record lists enrollment of 501 and a completed study. The study compared fezolinetant 30 mg and 45 mg with placebo during a 12-week double-blind period, followed by a non-controlled extension treatment period. The registry describes treatment through week 52. Because the extension was non-controlled, the primary placebo comparison is the double-blind comparison, not the later treatment period.

Participants recorded hot flashes using an electronic handheld device. Before treatment, the diary record for the 10 days immediately before randomization was used to establish baseline and confirm the symptom-frequency eligibility criterion. Moderate symptoms were defined by heat with sweating or dampness while activity could continue; severe symptoms disrupted activity. At night, the registry definitions distinguish whether action beyond rearranging bed sheets was needed.

For the primary endpoint, the full analysis set included randomized participants who took at least one dose and had data at the specified time point. The reported numbers contributing to the week 4 endpoint were 151 for placebo, 155 for fezolinetant 30 mg, and 155 for fezolinetant 45 mg. Enrollment and endpoint analysis counts are not interchangeable: the primary outcome population is defined by treatment exposure and available data at that time point.

In the extension, participants initially assigned placebo were re-randomized to fezolinetant 30 mg or 45 mg, while participants assigned active treatment continued their assigned dose. These later groups therefore reflect different prior treatment histories. The registry record does not report the original sample-size justification, detailed allocation procedures, or the complete statistical analysis plan.

4. Participant Flow and Accounting

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

Before assignment: Prior to randomization, participants had a screening period during which a minimum 10-day collection of baseline VMS frequency and severity assessments were performed.

Double-blind Period (12 Weeks)

Reasons for not completing this period:

Extension Period (40 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) (consisted of all randomized participants who took at least 1 dose of study intervention) with available data at specified time point.

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.

Population: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in The Mean Frequency of Moderate to Severe VMS at Week 4, measured over Baseline and week 4.

The primary endpoint was change from baseline in the mean frequency of moderate to severe vasomotor symptoms at week 4, measured in VMS per day. The frequency is the number of moderate or severe symptoms within 24 hours; a daily frequency for a week was derived as the mean of the available data over 7 days. Baseline was the average daily number based on non-missing values from the 10 days immediately before randomization.

A change score compares a participant’s follow-up frequency with that participant’s baseline frequency. A negative change indicates a lower recorded frequency at follow-up than at baseline. The registry reports least-squares mean changes and standard errors for each treatment group. Least-squares means are model-based group estimates, rather than simple arithmetic averages, and the standard error describes the estimated precision of a group mean.

Frequency is a direct measure of how often the target symptoms occurred, and the registry’s daily diary approach captures repeated reports rather than relying solely on later recall. The endpoint is specific: it measures frequency at week 4, not symptom severity, sleep, overall quality of life, or persistence of change across the entire study. The registry identifies the full analysis set as randomized participants who received at least one dose and had data at the specified time point. The precise handling of missing diary entries beyond the baseline derivation is not reported in the registry record.

7. Results Posted in the Registry

• Double-blind Period: Fezolinetant 30 mg: mean -5.53 versus -3.72 on control; difference -1.81 (95% CI -2.72 to -0.90), standardized effect d = -0.44; z-test p = <0.001.
• Double-blind Period: Fezolinetant 45 mg: mean -6.26 versus -3.72 on control; difference -2.54 (95% CI -3.45 to -1.63), standardized effect d = -0.62; z-test p = <0.001.

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.

Change From Baseline in The Mean Patient-reported Outcomes Measurement Information System Sleep Disturbance - Short Form 8b (PROMIS SD SF 8b) Total Score at Week 12

• 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 errors.
• Result:
  • Double-blind Period: Fezolinetant 30 mg: mean -4.10 versus -3.40 on control; difference -0.70 (95% CI -2.09 to 0.69), standardized effect d = -0.12; z-test p = 0.322.
  • Double-blind Period: Fezolinetant 45 mg: mean -5.50 versus -3.40 on control; difference -2.10 (95% CI -3.49 to -0.71), standardized effect d = -0.35; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Period: Fezolinetant 30 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Double-blind Period: Fezolinetant 45 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in The Mean Frequency of Moderate, and Severe VMS at Week 24

• 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:
  • Double-blind Period: Fezolinetant 30 mg/Extension Period: Fezolinetant 30 mg: mean -7.86 versus -9.01 on control; difference 1.15 (95% CI -0.46 to 2.76), standardized effect d = 0.24; z-test p = 0.162.
  • Double-blind Period: Fezolinetant 45 mg/Extension Period: Fezolinetant 45 mg: mean -7.96 versus -9.01 on control; difference 1.05 (95% CI -0.58 to 2.68), standardized effect d = 0.21; z-test p = 0.208.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Period: Fezolinetant 30 mg/Extension Period: Fezolinetant 30 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Period: Fezolinetant 45 mg/Extension Period: Fezolinetant 45 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in The Mean Severity of Moderate, and Severe VMS at Week 24

• 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:
  • Double-blind Period: Fezolinetant 30 mg/Extension Period: Fezolinetant 30 mg: mean -0.85 versus -0.78 on control; difference -0.07 (95% CI -0.33 to 0.19), standardized effect d = -0.08; z-test p = 0.597.
  • Double-blind Period: Fezolinetant 45 mg/Extension Period: Fezolinetant 45 mg: mean -0.90 versus -0.78 on control; difference -0.12 (95% CI -0.37 to 0.13), standardized effect d = -0.15; z-test p = 0.349.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Period: Fezolinetant 30 mg/Extension Period: Fezolinetant 30 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Period: Fezolinetant 45 mg/Extension Period: Fezolinetant 45 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover distinct aspects of symptoms and related experience, including sleep disturbance, frequency, severity, percentage reductions, and outcomes at later time points. The posted results do not form a single interchangeable measure: sleep scores, symptom counts, symptom severity, and the proportion reaching a reduction threshold address different questions. Their interpretation depends on the endpoint definition, assessment time, and analysis population.

At week 12, the registry reports sponsor MMRM results for sleep disturbance. The 30 mg comparison with placebo has a reported p-value of 0.381, while the 45 mg comparison has a reported p-value of 0.007. The summary-statistic recalculation for the 30 mg contrast has a confidence interval that includes zero; for 45 mg, the recalculated interval does not. As with the primary endpoint, the sponsor’s reported analysis is distinct from the simple recalculation. The registry also posts week 24 mean changes in frequency and severity, but no sponsor-reported analyses for those outcomes are listed in the registry record of the registry record.

These secondary findings provide context around the primary frequency result, but they should not be treated as confirmatory evidence on their own. When many outcomes, time points, and comparisons are examined, the chance of apparently notable results arising by chance can increase unless the testing strategy addresses multiplicity. The registry lists 14 outcome measures and 130 analyses, but the full prespecified hierarchy and multiplicity plan are not reported in the registry record. Unadjusted secondary results therefore carry less weight than a clearly specified primary analysis with an appropriate inferential plan. The different endpoints and timeframes also prevent a simple overall conclusion from being drawn by counting which comparisons have smaller p-values.

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

• Change From Baseline in The Mean Patient-reported Outcomes Measurement Information System Sleep Disturbance - Short Form 8b (PROMIS SD SF 8b) Total Score at Week 12
• Change From Baseline in The Mean Frequency of Moderate, and Severe VMS to Each Study Week Up to Week 12
• Change From Baseline in The Mean Severity of Moderate, and Severe VMS to Each Study Week Up to Week 12
• Mean Percent Change in The Frequency of Moderate And Severe Vasomotor Symptoms From Baseline to Each Study Week Up to Week 12
• Number of Participants With Percent Reduction of >=50% in the Mean Frequency of Moderate and Severe VMS From Baseline to Each Study Week Up to Week 12
• Number of Participants With Mean Percent Reduction of 100% in The Mean Frequency of Moderate, and Severe VMS From Baseline to Each Study Week Up to Week 12
• Change From Baseline in The Mean Frequency of Moderate, and Severe VMS at Week 24
• Change From Baseline in The Mean Severity of Moderate, and Severe VMS at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric measure of symptom frequency expressed as VMS per day. For each treatment group, the registry reports a least-squares mean change and its standard error. A mean summarizes the group’s average change, while the standard error reflects how precisely that mean has been estimated. It is not a measure of the range of individual participant outcomes.

What does the group comparison estimate?

A comparison between a treatment group and placebo estimates the difference in their mean changes from baseline. The reported primary contrasts are -1.82 for fezolinetant 30 mg versus placebo and -2.55 for fezolinetant 45 mg versus placebo. A negative contrast means the estimated change was more negative in the active-treatment group. The contrast should not be confused with the within-group change: placebo also had a negative mean change, -3.72 VMS per day.

The sponsor’s reported analysis used MMRM, or a mixed model for repeated measures. In general, this type of model analyzes measurements collected at multiple time points while accounting for their repeated nature within participants. Its least-squares mean contrasts are model-based estimates. The registry record does not report the full model specification, covariates, covariance structure, or missing-data assumptions, so those details cannot be independently described.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the data and the stated statistical model at a specified confidence level. The sponsor reports 95% confidence intervals for both primary comparisons. For 30 mg, the interval extends from -2.73 to -0.91; for 45 mg, it extends from -3.45 to -1.64. Both reported ranges are entirely negative. An interval is not a guarantee that the true value falls within that particular range, and it does not describe the distribution of individual responses.

The registry also reports p-values from the MMRM analyses and Hochberg analyses. A p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of the analysis; it is not the probability that the null hypothesis is true. The MMRM p-values are reported as < 0.001 for both comparisons. The Hochberg results are reported separately. Because multiple comparisons can increase the chance of a false-positive finding when considered as a family, adjusted procedures such as Hochberg can be used to account for multiplicity. The complete prespecified testing strategy is not reported in the registry record.

What do the recalculations represent?

The recalculated primary contrasts use the posted group means and standard errors to form simple, unadjusted comparisons. These calculations are not a reproduction of the MMRM, which uses the study’s repeated observations and model specification. The recalculated estimates are -1.81 and -2.54, compared with the sponsor’s reported estimates of -1.82 and -2.55. This small numerical discrepancy is why the sponsor’s analysis takes precedence. The posted calculations are useful as a transparent check on the scale and direction of the group summaries, not as a replacement for the sponsor analysis.

For these recalculations, the pooled standard deviation is approximated from the standard errors and group sizes. In general, a standard deviation describes variability among individual observations, while a standard error describes uncertainty in a mean. Recovering a standard deviation from a standard error depends on the sample size and calculation assumptions. The resulting pooled variability is therefore an approximation for the primary comparisons, not a directly reported participant-level spread.

Why does variability matter?

More variability makes a group mean less precise when the number of observations is fixed, and a smaller difference is harder to distinguish from random variation than a larger one under comparable conditions. Over-dispersion is a general concern when count outcomes vary more than a simple statistical model expects: if ignored, uncertainty can be understated. The registry provides no over-dispersion assessment for this endpoint, so it is not possible to state whether it was considered.

Finally, the reported analysis population requires at least one dose and data at the specified time point. This defines who contributes to the endpoint but does not explain how unavailable follow-up measurements were handled in the model. That method, along with the original design assumptions and full analysis plan, is not reported in the registry record. Statistical interpretation must therefore distinguish what the registry explicitly reports from general properties of the methods.

11. Confidence Intervals and Precision

The sponsor reports 95% confidence intervals for the primary treatment contrasts. For fezolinetant 30 mg versus placebo, the estimated difference in change is -1.82 VMS per day, with an interval from -2.73 to -0.91. For fezolinetant 45 mg versus placebo, the estimate is -2.55, with an interval from -3.45 to -1.64. Both ranges are entirely on the negative side of zero, consistent with the reported p-values of < 0.001.

The intervals are estimates of uncertainty around the model-based group contrasts. They indicate a range of effect sizes compatible with the data and the MMRM analysis, rather than a range containing most individual participants’ responses. The 45 mg estimate is more negative than the 30 mg estimate in the reported comparisons, but the registry’s reported primary analyses compare each dose with placebo; they do not report a direct statistical comparison between the two fezolinetant doses. A difference between the two point estimates alone does not establish a dose-to-dose difference.

The recalculated estimates from the posted group summaries are -1.81 and -2.54. They differ slightly from the sponsor’s reported values, and the sponsor’s analysis takes precedence. The recalculations rely on unadjusted summary-statistic methods and approximate variability rather than the full model-based analysis. Precision should therefore be judged primarily from the sponsor’s reported confidence intervals, while recognizing that the registry record does not provide the full model specification or all assumptions needed for independent reproduction.

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 illustrations express required sample sizes as participants per arm for 80% power and participants per arm for 90% power. These are not total numbers across both arms and are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration uses a specified fraction of the observed effect as the effect to detect. Time-to-event outcomes, if present, would use total events, but these continuous outcomes are expressed as participants per arm.

In plain terms, the 80% power column gives the estimated number of participants in each arm under those assumptions for an 80% chance of detecting the chosen effect if that effect is true. The 90% column uses a higher chance of detection and consequently requires more participants under the same general setup. Planning for 75% or 50% of the observed effect asks what sample size would be needed to detect a smaller effect than the observed one. Smaller effects need more participants because they are harder to distinguish from random variation.

The listed sizes are planning illustrations based on the observed effect, not the trial’s own original design calculations. The original sample-size justification and assumptions are not reported in the registry record. These figures are not observed power: observed power is not an appropriate way to reinterpret the results after the trial. The illustrations also do not establish that the trial was designed around these calculations or that the assumptions match the sponsor’s MMRM analysis.

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 = -1.810; pooled standard deviation σ = 4.082.
2. n = 2 × (1.96 + 0.842)² × 4.082² / -1.810² = 79.8, rounded up to 80 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 <- -1.81                      # observed difference in means
sigma <- 4.08222559267291                     # 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(4003142)
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 = 80 (80% power), 107 (90% power)
 75% of observed effect: n per arm = 142 (80% power), 191 (90% power)
 50% of observed effect: n per arm = 320 (80% power), 428 (90% power)
power.t.test: 80.8 
Simulated power at n = 80 per arm: 0.793 (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 sponsor’s primary analyses use MMRM and report a least-squares mean difference of -1.82 for fezolinetant 30 mg versus placebo, with a 95% confidence interval from -2.73 to -0.91 and p < 0.001. For 45 mg versus placebo, the reported difference is -2.55, with a 95% confidence interval from -3.45 to -1.64 and p < 0.001. The registry also lists Hochberg analyses with p = 0.049 and p < 0.001 for those respective comparisons.

The posted recalculations use unadjusted comparisons of the group summaries and produce estimates of -1.81 and -2.54. They are close to, but do not exactly match, the sponsor’s model-based estimates. This is expected to be possible because the recalculations do not reproduce the MMRM, its repeated-measures structure, or its model assumptions. The recalculated values are a supplementary check, not an alternative primary analysis.

Because the registry record identifies a discrepancy between the sponsor-reported results and recalculations, the sponsor’s own analysis takes precedence. The registry does not report enough detail to reproduce the model or fully assess its assumptions. The reported confidence intervals and p-values should therefore be read as the sponsor’s stated inferential results, with the recalculations used only as an approximate summary-statistic comparison.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines multiple outcomes, treatment groups, or time points. If each comparison is considered independently, the chance of at least one false-positive result across a family of tests can increase. A prespecified testing hierarchy or an adjustment procedure can help control this issue, but interpretation requires knowing which hypotheses were included, their order, and how the procedure was applied.

The registry record lists 14 outcome measures and 130 analyses. It reports MMRM results for the two primary comparisons and separate Hochberg results, with p = 0.049 for the 30 mg comparison and p < 0.001 for the 45 mg comparison. Hochberg is a method for adjusting p-values across a defined family of tests. However, the full protocol-level multiplicity strategy, testing hierarchy, and specification of the family are not reported in the registry record. The posted Hochberg values should be recognized as reported analyses without assuming how every secondary outcome was handled.

The primary population is described as randomized participants who took at least one dose and had data at the specified time point. Baseline frequency used non-missing diary values from the 10 days before randomization. These details clarify the primary endpoint definition and population, but they do not explain how missing outcome data after randomization were handled. The MMRM is reported, yet its missing-data assumptions and sensitivity analyses are not reported in the registry record. It is therefore not possible to assess from the registry alone how robust the findings are to different assumptions about unavailable measurements.

The original sample-size justification, any interim analyses, and the complete statistical analysis plan are also not reported in the registry record. This limits independent assessment of whether the endpoint, analysis population, model, and multiplicity adjustments were fully specified before results were examined. The absence of these details does not itself show that the analyses were inappropriate; it means that those design and analysis features cannot be confirmed from 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hepatotoxicity (1.3%), foot fracture (1.3%), multiple injuries (1.3%), uterine leiomyoma (1.3%), atrial fibrillation (1.3%).

During the double-blind period and extension group reporting, the registry lists the numbers at risk and the number of participants affected by serious adverse events. The placebo group lists 0 affected among 167 at risk. The group receiving fezolinetant 30 mg through the extension lists 9 among 166, and the group receiving fezolinetant 45 mg through the extension lists 8 among 167. The placebo-to-fezolinetant 30 mg extension group lists 2 among 76, and the placebo-to-fezolinetant 45 mg extension group lists 4 among 75. One death is listed in the latter group; the other groups list 0 deaths.

These are participant counts, not counts of every event, and the treatment histories and observation periods differ across the listed groups. In particular, the placebo extension groups began with placebo before receiving fezolinetant, so they should not be read as continuous placebo controls. The registry lists several serious-event terms at 1.3% each, including hepatotoxicity and other terms, but the posted summary does not establish that treatment caused any particular event.

Serious adverse event counts describe reported events in the trial population; they do not by themselves determine comparative risk or establish causality. The counts should be interpreted alongside group sizes, exposure periods, and the registry’s definitions and reporting practices. Detailed case-level information and causal assessments are not reported in the registry record.

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

The primary result describes a difference in mean change in recorded moderate to severe hot-flash frequency at week 4 between each fezolinetant group and placebo. The sponsor’s reported estimates are negative, and the reported 95% confidence intervals lie below zero. This is a statistical description of the posted endpoint data under the sponsor’s analysis, not a guarantee about the experience of any individual participant.

The result does not say that all participants had the same change, or that every participant improved. Group averages do not show the full distribution of individual responses. Nor does the primary endpoint establish the magnitude of changes in symptom severity, sleep, or other outcomes. Those questions require separate endpoint-specific results and analysis.

The week 4 comparison does not, on its own, establish how long an observed difference persists. The study included an extension, but it was non-controlled and included participants who switched from placebo to active treatment. Later results therefore do not have the same concurrent placebo comparison as the double-blind phase. The primary endpoint also does not answer whether an effect continues beyond the time point it measures.

Statistical significance is not the same as clinical importance. The registry record does not provide a threshold for a clinically meaningful difference in daily symptom frequency, so the reported estimates cannot be classified against such a threshold from these registry entries alone. Likewise, a p-value is not the probability that the result occurred by chance or that a treatment is effective.

Finally, the registry record does not report the complete statistical analysis plan, original sample-size justification, or detailed missing-data assumptions. These limits matter when judging how completely the posted results can be independently assessed. The findings should be understood as the reported statistical comparisons for a defined population and time point, not as a complete account of every potential benefit, risk, or longer-term outcome.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and the comparison group matter. The primary question is a week 4 difference in change from baseline, not simply whether symptom frequency declined within an active-treatment group. The placebo group also showed a negative mean change, so interpreting only within-group changes would omit the randomized comparison that addresses differences between groups.

It also demonstrates the distinction between a sponsor’s model-based analysis and a simple recalculation from summary statistics. The reported MMRM estimates and the recalculated contrasts are close but not identical. A model that uses repeated measurements is not recreated by comparing group means and standard errors alone. The sponsor’s own reported analysis therefore takes precedence when the registry identifies a discrepancy.

The trial’s many outcomes and analyses make multiplicity an important consideration. The registry reports both MMRM and Hochberg analyses for the primary comparisons, but does not supply the complete testing plan. This illustrates why p-values are most informative when read alongside a prespecified endpoint hierarchy, adjustment method, and analysis population.

Finally, the design changes after the controlled phase: placebo participants are re-randomized to active treatment and the extension is non-controlled. Later observations can contribute information about outcomes over time, but they do not provide the same randomized placebo contrast as the first 12 weeks. Distinguishing the controlled and extension periods is essential to interpreting what each set of results can answer.

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 primary result is limited to the week 4 endpoint and the participants with available data at that specified time point. The registry does not report the detailed amount or pattern of missing follow-up data, the method used to address missingness, or sensitivity analyses. Although the analysis population is defined and MMRM is named, the model specification and assumptions are not reported in the registry record.

The recalculated estimates are based on summary statistics and approximate pooled variability. They are not participant-level analyses and do not reproduce the sponsor’s MMRM. The small differences from the sponsor estimates underscore that they should not be treated as an independent validation of the reported model.

The registry lists many outcomes and analyses, while the full multiplicity plan is not reported. This makes it difficult to determine which secondary findings were confirmatory and how the full family of tests was handled. Some posted secondary outcomes have sponsor analyses listed, while others do not. Their evidence strength should not be assumed to match the primary endpoint.

Later extension outcomes are non-controlled and involve different treatment histories, including participants who switched from placebo. They cannot be interpreted as though all groups remained randomized to active treatment versus concurrent placebo throughout the extension. The posted safety groups also reflect different exposure histories and durations, so direct comparisons of their counts require caution.

The registry record does not report the original sample-size justification, interim-analysis plans, or full protocol and statistical analysis plan. It also does not give a clinically meaningful threshold for the primary symptom-frequency difference. These gaps constrain independent evaluation of design choices, robustness, and clinical importance. They do not establish that a particular bias occurred, but they limit what can be concluded from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Find Out if Fezolinetant Helps Reduce Moderate to Severe Hot Flashes in Women Going Through Menopause - 2 — NCT04003142.
• Registry record last updated 2024-11-05; status last verified 2024-10.
• Results first posted 2022-06-15.
• 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 3 randomized, double-blind, placebo-controlled study of fezolinetant 30 mg and 45 mg in women with moderate to severe hot flashes associated with menopause. The placebo-controlled double-blind period lasted 12 weeks and was followed by a non-controlled extension. Enrollment was 501.

The primary outcome was change from baseline in mean daily frequency of moderate to severe vasomotor symptoms at week 4. The sponsor reported MMRM differences versus placebo of -1.82 for 30 mg and -2.55 for 45 mg; both reported p-values were < 0.001. The registry also lists Hochberg results for these comparisons. Summary-statistic recalculations differ slightly, so the sponsor’s reported analysis takes precedence.

The record includes secondary outcome and safety information, but the complete multiplicity strategy, missing-data assumptions, original sample-size justification, and full statistical analysis plan are not reported in the registry record. Extension results are non-controlled and should be distinguished from the randomized placebo comparison.