A Study to Assess the Efficacy and Safety of HMI-115 in Subjects With Endometriosis-Associated Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Efficacy and Safety of HMI-115 in Subjects With Endometriosis-Associated Pain (NCT05101317), a randomized phase 2 study. The primary outcome is Change in Dysmenorrhea (DYS) Measured by Numeric Rating Scale (NRS) From Baseline to Week 12 (Percentage Change).

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, multicenter, double-blind, placebo-controlled Phase 2 study of HMI-115 for moderate to severe endometriosis-associated pain. It records quadruple masking. These design labels describe the trial structure, but the registry record does not report which roles were masked or the practical procedures used to maintain masking. The sponsor is Hope Medicine (Nanjing) Co., Ltd.

Participants were assigned to HMI-115 60mg, HMI-115 120mg, HMI-115 240mg, or placebo. Each was given by subcutaneous injection once every 2 weeks. The primary endpoint was assessed from baseline to Week 12, matching the stated 12-week treatment period. Several listed secondary outcomes extend follow-up to Week 24. The registry does not report details of treatment after the 12-week period or explain how those later assessments were handled.

The study began on 2021-10-11, had a primary completion date of 2024-09-26, and is marked completed. The registry reports enrollment of 142. That enrollment figure is not necessarily the denominator for a particular endpoint: the posted primary outcome includes arm-specific analysis counts, and the safety results use their own at-risk counts. Those outcome-specific denominators should be read alongside the corresponding results rather than inferred from overall enrollment.

The registry record does not report the trial’s original sample-size justification, allocation ratio, randomization procedure, detailed eligibility criteria, or full statistical analysis plan. It also does not report an interim-analysis plan. The study design can therefore be described from its registered labels and treatment arms, but some operational and analytical details remain unavailable in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 1\. Screening Period: up to 75 days prior to first dose * Screening Visit 1 * Screening Visit 2 (at least 35 days before Visit 3 to ensure at least 5 weeks Baseline pain score obtained before randomization)

Week1-13

Reasons for not completing this period:

Week 13-25

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: PAS: All randomized subjects with at least 1 dose with surgical diagnosis

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: PAS：All subjects in the FAS(All randomized subjects who take at least one dose of IMP) who have surgical diagnosis.

6. Primary Endpoint

The registry lists the primary outcome as Change in Dysmenorrhea (DYS) Measured by Numeric Rating Scale (NRS) From Baseline to Week 12 (Percentage Change), measured over Baseline, Week 12.

The primary endpoint is the percentage change from baseline to Week 12 in dysmenorrhea, or menstrual pain, measured by the Numeric Rating Scale. The registry describes the scale as ranging from 0, no pain, to 10, severe pain, with higher scores indicating worse pain. A negative percentage change represents a reduction relative to baseline; the scale description gives the direction in which pain severity is scored.

The endpoint focuses on change rather than the Week 12 score alone. Comparing change from baseline can account for differences in starting scores, while the randomized placebo group provides a concurrent reference for changes that may occur without active study treatment. The registry reports least-squares means and standard errors for the arm-level outcome. The posted results include 27 participants in each HMI-115 dose group and 30 in the placebo group for this endpoint.

The primary population is described as all randomized subjects with at least 1 dose and a surgical diagnosis. The registry record does not report the detailed model used to estimate the least-squares means, how missing Week 12 measurements were handled, or the clinical threshold considered important for this scale. Those details matter when interpreting what a difference in percentage change means. The endpoint captures one defined aspect of pain at one assessment time; it is not, by itself, a complete measure of symptoms, function, safety, or longer-term outcomes.

7. Results Posted in the Registry

• HMI-115 60mg: mean -27.35 versus -18.61 on control; difference -8.74 (95% CI -34.30 to 16.82), standardized effect d = -0.18; z-test p = 0.503.
• HMI-115 120mg: mean -34.72 versus -18.61 on control; difference -16.11 (95% CI -41.76 to 9.54), standardized effect d = -0.33; z-test p = 0.218.
• HMI-115 240mg: mean -41.57 versus -18.61 on control; difference -22.96 (95% CI -49.49 to 3.57), standardized effect d = -0.47; z-test p = 0.090.

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 in Dysmenorrhea (DYS) Measured by Numeric Rating Scale(NRS) From Baseline to Week 24 (Percentage Change)

• 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:
  • HMI-115 60mg: mean -6.86 versus 3.97 on control; difference -10.83 (95% CI -42.47 to 20.81), standardized effect d = -0.18; z-test p = 0.502.
  • HMI-115 120mg: mean -21.82 versus 3.97 on control; difference -25.79 (95% CI -57.62 to 6.04), standardized effect d = -0.42; z-test p = 0.112.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HMI-115 60mg 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 HMI-115 120mg and the control. The interval gives the range of effects that remain compatible with the data.

Change in Dysmenorrhea(DYS) Measured by Numeric Rating Scale (NRS) From Baseline to Week 24 (Absolute Score Change)

• 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:
  • HMI-115 60mg: mean -1.87 versus -1.45 on control; difference -0.42 (95% CI -1.96 to 1.12), standardized effect d = -0.14; z-test p = 0.592.
  • HMI-115 120mg: mean -2.95 versus -1.45 on control; difference -1.50 (95% CI -3.05 to 0.05), standardized effect d = -0.51; z-test p = 0.057.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HMI-115 60mg 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 HMI-115 120mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning dysmenorrhea, non-menstrual pelvic pain, dyspareunia, pain impact, rescue medication use, and menstrual period heaviness. Some are assessed as percentage change, others as absolute score change, and several include repeated or later assessments. This range can provide context beyond the primary Week 12 dysmenorrhea measure, but it also means that the evidence is distributed across distinct outcomes and time points.

In broad terms, the posted secondary results are not a single, uniform confirmation of the primary comparison. The reported pain outcomes vary in their estimates across doses and assessment times. They should be interpreted as additional descriptive evidence rather than as independent proof of a consistent treatment effect. The primary endpoint remains the central registered question; secondary patterns can help generate questions for further study but do not resolve the uncertainty in the primary comparison.

The registry record reports nine secondary outcomes, while the number of posted outcome measures is 11. It lists no reported analyses for the secondary comparisons included in the recalculations. Not every listed secondary outcome has a complete comparison result in the record, and the record does not report a comprehensive model-based analysis across all secondary measures. Therefore, an overall pattern should not be reduced to selecting the most favorable-looking endpoint or time point.

General explanation: When many outcomes, doses, and visits are examined, some estimates may look unusual by chance even if there is no underlying effect. Unadjusted tests do not account for that multiplicity and can overstate the strength of evidence if treated as confirmatory. The registry record does not report a multiplicity adjustment or testing hierarchy. Consequently, unadjusted secondary results carry less weight than a prespecified, appropriately analyzed primary outcome, particularly when their uncertainty is not fully reported.

Secondary findings are most useful when considered alongside their measurement definitions, timing, uncertainty, missing-data handling, and the trial’s planned analysis strategy. Since several of those details are not reported in the registry record, the secondary outcomes provide limited grounds for strong conclusions beyond describing the recorded estimates.

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

• Change in Dysmenorrhea (DYS) Measured by Numeric Rating Scale(NRS) From Baseline to Week 24 (Percentage Change)
• Change in Non-menstrual Pelvic Pain (NMPP) Measured by Numeric Rating Scale (NRS) From Baseline to Week 12 and 24 (Percentage Change)
• Change in Dyspareunia (DYSP) Measured by NRS From Baseline to Week 12 and 24 (Percentage Change)
• Change From Baseline (CFB) in the Monthly Mean Endometriosis Daily Impact Pain Scale for DYS, NMPP and DYSP
• Change From Baseline (CFB) by Visit in Permitted Rescue Medication Use
• Change in Menstrual Period Heaviness (Bleeding) From Baseline by Visit
• Change in Dysmenorrhea(DYS) Measured by Numeric Rating Scale (NRS) From Baseline to Week 24 (Absolute Score Change)
• Change in Non-menstrual Pelvic Pain (NMPP) Measured by Numeric Rating Scale (NRS) From Baseline to Week 12 and 24 (Absolute Score Change)

9. Statistical Interpretation

10. Statistical Methods Explained

General explanation: A randomized, parallel-group study assigns participants to separate treatment groups and compares outcomes across those groups. Randomization is intended to make groups comparable on average at the beginning of the study, including on factors that were not measured. It does not guarantee that every group will have identical baseline characteristics, especially when group sizes are limited. A placebo group provides a concurrent comparison for changes that might occur over time, reflect expectations, or arise from assessment and study participation.

The registry reports least-squares means for the primary endpoint. In general, a least-squares mean is a model-based estimate of a group average, often adjusted for variables included in the model. The registry record does not identify the variables or model specification used to produce these estimates, so the exact adjustment cannot be described. The accompanying standard errors quantify uncertainty around the estimated arm-level means; they are not the same as the spread of individual participant responses.

The primary measure is percentage change from baseline. In general, percentage change expresses a change relative to a starting value, so the same absolute change can correspond to different percentages for different baseline values. For a pain score, negative change indicates a decline relative to baseline. Because the primary result is a least-squares mean, it should be understood as a model-based summary, not as a statement that every participant experienced the average change.

How should the dose-placebo estimates be read?

The comparison estimates are unadjusted recalculations based on the posted arm-level means and standard errors. Each estimate is the HMI-115 arm minus the placebo arm for the corresponding outcome. A negative estimate means the estimated percentage change was more negative in the HMI-115 group. That direction alone does not establish a meaningful benefit or a causal effect. The recalculations do not reproduce an unpublished sponsor model, and the registry lists no reported analyses for these comparisons.

The recalculated intervals use approximate standard deviations derived from the reported standard errors. This is a simplifying assumption because the source results are model-based least-squares means rather than raw group means with reported standard deviations. The recalculated comparisons therefore provide an approximate, unadjusted view of uncertainty. They should not be treated as a substitute for the trial’s prespecified analysis.

What does a p-value contribute?

General explanation: A p-value describes how compatible 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, and it does not measure the size or clinical importance of an effect. The listed p-values are unadjusted recalculations. Because the trial has multiple dose comparisons and multiple outcomes, these values do not account for the full set of possible comparisons.

Confidence intervals are useful alongside p-values because they show a range of values compatible with the data under the calculation’s assumptions. When an interval includes no difference, the data do not clearly distinguish that estimate from no difference at the conventional reference point. An interval that includes no difference can still contain potentially relevant effects in either direction; its width indicates how much uncertainty remains. The primary intervals are wide, so they do not support a precise estimate of the dose-placebo differences.

Why do analysis populations and missing data matter?

The primary population is described as all randomized subjects with at least 1 dose and a surgical diagnosis. This is not necessarily identical to every possible analysis population, such as all randomized participants regardless of dose or participants with a measured outcome. The registry record does not report the participant flow for the endpoint, the amount or pattern of missing data, or the method used to address missing values. If missingness differs across groups or relates to pain outcomes, the analyzed results may not represent the randomized groups in the same way.

More generally, analysis choices can affect estimates and uncertainty. Covariate adjustment, repeated-measure modeling, assumptions about missing observations, and the handling of multiple comparisons can all influence reported results. These are general considerations, not claims about what was done in this trial. The registry record does not report enough detail to assess those choices.

How should the secondary outcomes be considered?

The registered secondary outcomes cover additional pain measures, percentage and absolute score changes, pain impact, rescue medication use, and menstrual bleeding. They extend assessment to Week 24 for some outcomes and include assessments by visit for others. In general, multiple outcomes can provide a broader view of the experience being studied, but they also create more opportunities for apparently notable results to arise by chance. A prespecified testing hierarchy or multiplicity adjustment can help control that issue. Neither is reported in the registry record. Secondary results should therefore be treated as supportive and exploratory unless a fuller analysis plan establishes otherwise.

11. Confidence Intervals and Precision

The recalculated 95% confidence intervals for the Week 12 primary comparisons are wide. For HMI-115 60mg versus placebo, the estimate is -8.74 and the interval extends from -34.3 to 16.82. For HMI-115 120mg versus placebo, the estimate is -16.11 and the interval extends from -41.76 to 9.536. For HMI-115 240mg versus placebo, the estimate is -22.96 and the interval extends from -49.49 to 3.57. Each interval includes no difference and allows values on both sides of it.

General explanation: A confidence interval expresses uncertainty around an estimate under the assumptions used to calculate it. A narrower interval indicates greater precision; a wider interval indicates that a broader range of effects remains compatible with the data. It is not a guarantee that the true effect lies inside the interval, nor does it show the probability that a particular effect is true.

Here, the intervals do not pin down the size or direction of the dose-placebo differences. The point estimates lean toward more negative percentage change in the HMI-115 groups, but the intervals also include estimates in the opposite direction. The results therefore do not precisely distinguish the observed pattern from no difference. The arm-level primary results have standard errors of 9.568, 9.63, 10.23, and 8.859 for HMI-115 60mg, HMI-115 120mg, HMI-115 240mg, and placebo, respectively.

These comparison intervals are unadjusted recalculations from posted summary statistics, using approximate standard deviations derived from the reported standard errors. They are not sponsor-reported intervals, and the registry record lists no reported analyses for the comparisons. Their precision should be interpreted with that limitation in mind, as well as the absence of reported details about the primary model and missing-data handling.

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

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect if the assumptions hold. The 90% power column gives the corresponding number per arm for a design with a 90% chance. Power is a planning property of a proposed study under assumptions; it is not a measure of whether a result is true or important.

Rows planning for 75% or 50% of the observed effect consider effects smaller than the full observed estimate. Smaller effects are harder to distinguish from random variation, so they require more participants for the same target power under the same assumptions. The figures are sensitive to the observed effect and variability used in the illustration, and can change substantially if those estimates are unstable. These are not observed power calculations.

The plotted curve should be read in the same planning context: it illustrates how the required per-arm size varies with the effect used for planning under the stated assumptions. It does not describe the number of participants actually enrolled in each trial arm, nor does it establish what sample size would be appropriate without a prespecified clinically meaningful target and a justified variance estimate.

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 = -8.740; pooled standard deviation σ = 49.091.
2. n = 2 × (1.96 + 0.842)² × 49.091² / -8.740² = 495.2, rounded up to 496 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 <- -8.74                      # observed difference in means
sigma <- 49.0908187153714                     # 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(5101317)
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 = 496 (80% power), 663 (90% power)
 75% of observed effect: n per arm = 881 (80% power), 1,179 (90% power)
 50% of observed effect: n per arm = 1,981 (80% power), 2,652 (90% power)
power.t.test: 496.2 
Simulated power at n = 496 per arm: 0.803 (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. Multiplicity, Missing Data and Analysis Populations

The trial has a primary endpoint, multiple HMI-115 dose groups, and a broad set of secondary outcomes at different time points. This creates a multiplicity issue: repeated testing across doses, outcomes, and visits increases the chance that at least one unadjusted result will appear noteworthy by chance. The recalculated p-values are unadjusted. The registry record does not report a prespecified testing hierarchy, a multiplicity correction, or how the primary comparisons were intended to be interpreted across the three dose groups.

The absence of a reported multiplicity plan does not establish that no such plan existed outside the registry. It means the registry record does not allow readers to verify whether the comparisons were confirmatory, how error rates were controlled, or whether some analyses were considered exploratory. Secondary outcomes should accordingly be read cautiously, especially if attention is directed to isolated estimates rather than the full outcome set.

The primary analysis population is described as all randomized subjects with at least 1 dose and a surgical diagnosis. The registry record does not explain why these criteria define the population, how many randomized participants were excluded from it, or whether additional populations were used for efficacy or safety analyses. It also does not report participant disposition by reason for withdrawal or outcome.

Missing-data methods are not reported in the registry record. This leaves unanswered how unavailable Week 12 assessments were handled, whether the model used all available repeated measurements, and what assumptions were made about participants with missing outcomes. Missingness can affect both estimated treatment differences and their precision, particularly if reasons for missing assessments are related to treatment or pain outcomes. These are methodological concerns, not evidence that missing data biased the results in a particular direction.

The detailed statistical analysis plan, including covariate adjustment and model specification, is also not reported in the registry record. Without those details, the posted least-squares means cannot be fully reconstructed and the recalculated comparisons remain approximate, unadjusted summaries rather than a substitute for the trial’s prespecified analysis.

15. 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: breast mass (4.2%).

The safety record gives serious adverse events for each arm using an at-risk denominator. There were 0 serious adverse events among 27 participants in the HMI-115 60mg group, 0 among 27 in the HMI-115 120mg group, 1 among 24 in the HMI-115 240mg group, and 0 among 30 in the placebo group. The registry lists 0 deaths in every group. The serious-event term listed among the top terms is Breast mass, at 4.2%.

These counts are descriptive. The single serious adverse event appears in the HMI-115 240mg group; the registry summary does not establish whether it was caused by study treatment. The listed term and percentage should be read as the registry reports them, without inferring a broader pattern from one term or a small number of events.

The record also reports other adverse events affecting 15 participants in the HMI-115 60mg group, 16 in the HMI-115 120mg group, 18 in the HMI-115 240mg group, and 11 in the placebo group. These are counts of participants affected, not a measure of event severity. The registry summary does not provide enough detail to compare event types, duration, recurrence, or attribution comprehensively. Absence of a reported serious event in an arm is not proof that no risk exists.

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

The primary results describe average percentage change in dysmenorrhea scores from baseline to Week 12 among the reported analysis population. The HMI-115 groups had more negative estimated changes than placebo, and the recalculated dose-placebo differences were negative. However, all three recalculated 95% confidence intervals include no difference and extend into positive values. The posted summaries therefore leave substantial uncertainty about the size and direction of the treatment-placebo differences.

These results do not establish that HMI-115 improves pain, nor do they establish that it has no effect. A point estimate is not a definitive answer, and a nonsignificant unadjusted p-value is not proof of equivalence or absence of an effect. The intervals allow a range of possible differences, while the available registry entries do not support a full reconstruction of the sponsor’s planned analysis.

The results also do not establish whether any difference is clinically meaningful. The registry provides the scale range and direction, but does not report a threshold for a meaningful change or enough baseline detail to translate the percentage-change estimates into a complete account of participants’ experiences. Group averages can also conceal variation in individual responses.

The primary assessment concerns one symptom at Week 12. It does not represent every dimension of endometriosis-associated pain, other symptoms, functioning, or longer-term outcomes. Secondary outcomes add context, but their multiplicity and incomplete analysis details limit confirmatory interpretation. Safety counts are likewise descriptive and do not determine causality or characterize all possible risks.

The findings apply to the registered study population and methods as documented. The registry record does not report enough about eligibility, missing data, analysis choices, or the full statistical plan to assess all sources of uncertainty. Further interpretation requires the complete trial report and its prespecified analyses; the registry summaries alone should not be treated as a clinical recommendation.

17. Why This Trial Matters Statistically

This trial illustrates several important statistical features of a multi-arm study. The primary outcome compares three dose groups with one placebo group, creating several treatment-placebo contrasts rather than a single comparison. The numerical estimates show a pattern across listed doses, but uncertainty around each estimate is broad. A sequence of point estimates should not be mistaken for evidence of a dose-response relationship without an appropriate planned analysis.

It also shows why an arm-level change and a treatment contrast answer different questions. Each least-squares mean describes an estimated change within one group. The mean difference compares that change with the placebo group. Looking only at the within-group values could overstate what can be attributed to treatment, because change also occurs in the placebo group.

The trial further demonstrates the importance of precision. The recalculated confidence intervals include no difference for each primary dose comparison and allow effects in either direction. The point estimates alone provide an incomplete account; the intervals convey how uncertain their magnitude remains.

Finally, the registry records multiple secondary measures, extended follow-up for some outcomes, and safety summaries. Such breadth can be informative, but interpretation depends on the planned analysis, multiplicity handling, outcome completeness, and missing-data approach. Those details are not reported in the registry record. The statistical lesson is to distinguish registered questions from exploratory patterns, arm-level summaries from contrasts, and descriptive safety counts from evidence of causality.

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 limitation is that the registry record does not report the detailed statistical analysis plan. The model behind the least-squares means, any covariate adjustments, the handling of repeated measures, and the intended multiplicity strategy are not available. The recalculated comparisons are unadjusted approximations from summary statistics and may not match the sponsor’s planned analysis.

The record does not report missing-data methods or participant flow for the primary endpoint. Although arm-specific analysis counts are listed, the reasons participants may not have contributed data and the assumptions used for any missing observations are not described. This restricts assessment of whether the analyzed groups represent the randomized groups.

The primary outcome uses percentage change, but the record does not include individual-level data or enough baseline information to examine how starting pain scores relate to the reported changes. It also does not report a threshold for a clinically important difference. The estimates therefore cannot be translated directly into the proportion of participants who experienced a meaningful improvement.

The comparisons have wide confidence intervals, and the sample-size illustrations are based on observed effects rather than the original design rationale. The registry does not report that original rationale, so it is not possible to assess the intended detectable effect from the record alone. The listed secondary outcomes introduce additional interpretive complexity because no multiplicity plan is reported.

Finally, registry summaries do not provide the detail needed to assess all aspects of safety, adherence, outcome measurement, or generalizability. These limitations identify what the record cannot establish; they do not show that any particular unreported method was inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Assess the Efficacy and Safety of HMI-115 in Subjects With Endometriosis-Associated Pain — NCT05101317.
• Registry record last updated 2026-01-21; status last verified 2026-01.
• Results first posted 2025-11-18.
• 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 registry describes a completed randomized, multicenter, double-blind, placebo-controlled Phase 2 study of HMI-115 for moderate to severe endometriosis-associated pain. It records quadruple masking, parallel groups, enrollment of 142, and a 12-week treatment period. Participants received HMI-115 60mg, 120mg, or 240mg, or placebo, by subcutaneous injection once every 2 weeks.

The primary outcome was percentage change in dysmenorrhea measured by Numeric Rating Scale from baseline to Week 12. The posted least-squares mean changes were more negative in each HMI-115 group than in placebo. Recalculated, unadjusted dose-placebo estimates had confidence intervals that included no difference and were imprecise.

The record includes secondary outcomes and descriptive safety counts, but does not report the detailed statistical analysis plan, multiplicity approach, or missing-data methods. Its summary results therefore support cautious description rather than definitive conclusions about treatment effects.