A Study to Compare Efficacy, PK, PD, Safety and IMM of MB09 to Prolia® [EU-sourced] in Postmenopausal Osteoporosis.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Compare Efficacy, PK, PD, Safety and IMM of MB09 to Prolia® [EU-sourced] in Postmenopausal Osteoporosis. (NCT05338086), a randomized phase 3 study. The primary outcome is Efficacy: Percentage Change From Baseline (%CfB) in Lumbar Spine Bone Mineral Density (LS-BMD) at 52 Weeks - Modified Full Analysis Set (mFAS).

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel, multicenter, multinational phase 3 study. The registry record lists quadruple masking and an enrollment of 558. It describes the study as comparing efficacy, pharmacokinetics, pharmacodynamics, safety, and immunogenicity of MB09 with EU-Prolia in postmenopausal women with osteoporosis. The listed study status is completed; the start date is 2022-03-16 and the primary completion date is 2023-12-14.

Three treatment-group labels appear in the record: MB09-MB09, Prolia-MB09, and Prolia-Prolia. The MB09-MB09 and Prolia-Prolia descriptions specify injections every 6 months. The Prolia-MB09 description names that group but describes Prolia administration; the sequence and timing of treatments for this group are not fully explained in the registry record. Calcium and vitamin D are also listed as interventions, without further details about their use in the study description.

The primary comparison reported for the efficacy endpoint is between MB09 and EU-Prolia in the mFAS. The posted arm summaries include 233 participants for MB09 and 250 for EU-Prolia. Those outcome-analysis counts should not be conflated with the overall enrollment or with the safety denominators, which differ. The registry reports a main treatment period and a transition period for safety analyses, but detailed period definitions and participant flow are not reported in the registry record.

The primary endpoint was assessed from baseline through Week 52, also described as Month 12. Bone mineral density was assessed by dual-energy X-ray absorptiometry, with lumbar spine measurements from L1 to L4 taken at a central imaging vendor. The record lists further efficacy, pharmacokinetic, pharmacodynamic, safety, and immunogenicity outcomes, but detailed numerical results are not available for most of those outcomes in the information reported.

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: The study included the Screening Period (28 days before randomization) that began after the participants had signed the written informed consent form. On Day 1 of the Main Treatment Period (MTP), subjects were randomly assigned in a 2:1:1 ratio to one of the 3 arms to receive one subcutaneous (SC) injection of European Union (EU) Prolia or MB09. Only those subjects who tolerated the initial 2 doses received the third dose and proceeded to the Transition/Safety Follow-up Period (TP).

Main Treatment Period (Day1 to Month 12)

Reasons for not completing this period:

Transition Period (M12 to M18)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Full Analysis Set (mFAS) is a subset of subjects in the FAS who met all eligibility criteria. The mFAS term defined a set at the data point level which included a data record at each timepoint for all eligible subjects in the FAS but excluded data observed after the first occurrence of those intercurrent events (ICEs) where a hypothetical strategy was taken (eg, missing a dose, errors or deviations in dosing, or receipt of any prohibited therapies or other osteoporosis medication).

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: The Safety Analysis Set (SAF) consisted of all randomised subjects who received at least one administration of study treatment.

6. Primary Endpoint

The registry lists the primary outcome as Efficacy: Percentage Change From Baseline (%CfB) in Lumbar Spine Bone Mineral Density (LS-BMD) at 52 Weeks - Modified Full Analysis Set (mFAS), measured over Baseline (Screening), up to Week 52.

The primary endpoint is percentage change from baseline in lumbar spine bone mineral density (LS-BMD) at Week 52. It is a continuous measure: each participant’s follow-up measurement is considered relative to their baseline measurement, and the endpoint summarizes the resulting change across the analysis population. The reported unit is percentage change. The endpoint uses measurements of the lumbar spine from L1 to L4, assessed by dual-energy X-ray absorptiometry at a central imaging vendor.

Bone mineral density is the measured quantity in this endpoint; the analysis does not directly measure fractures or other clinical events. The stated objective was to compare MB09 with EU-Prolia and demonstrate equivalent efficacy at Week 52. A continuous endpoint can capture differences in the measured quantity across participants rather than reducing the outcome to whether a particular event occurred. In general, a comparison of group means describes the average contrast, while uncertainty estimates indicate how precisely that contrast is determined.

The primary analysis used a mixed model for repeated measures on composite percentage change data at Month 6 and Month 12, without imputation of missing data. The posted primary arm summaries are least-squares means with standard errors. These are model-based summaries, not simple raw means. The registry record does not report an equivalence margin, so the endpoint objective and analysis label can be described, but the threshold required to judge formal equivalence cannot be established from the record.

7. Results Posted in the Registry

• EU-Prolia: mean 5.66 versus 5.86 on control; difference -0.20 (95% CI -0.91 to 0.51), standardized effect d = -0.05; z-test p = 0.579.

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.

Efficacy: Percent Change From Baseline in Lumbar Spine Bone Mineral Density (LS-BMD) at Week 52 - Full Analysis Set (FAS)

• 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:
  • EU-Prolia: mean 5.38 versus 5.40 on control; difference -0.02 (95% CI -0.74 to 0.70), standardized effect d = -0.00; z-test p = 0.957.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EU-Prolia and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning lumbar spine, total hip, and femur neck bone mineral density; pharmacodynamics; pharmacokinetics; safety; and immunogenicity. It identifies 10 secondary outcomes as posted, but numerical summaries in the registry record are limited in the information available for interpretation. The secondary efficacy result with numerical detail uses the FAS and reports lumbar spine bone mineral density at Week 52. Its analysis is identified as ANCOVA and is labeled as an equivalence analysis.

At a broad level, the detailed secondary lumbar spine result is consistent with the primary comparison in that the posted estimates are close between the two treatment groups and the reported equivalence analysis does not indicate a large contrast. However, the primary and secondary analyses use different named populations and methods: the primary analysis uses the mFAS and MMRM, while this secondary analysis uses the FAS and ANCOVA. They are not duplicate estimates of exactly the same analysis, and the secondary result does not replace the prespecified primary endpoint.

In general, secondary outcomes help describe whether observations extend across related measures and other domains, but each outcome has its own measurement, population, and uncertainty. Multiple testing also matters. When many outcomes or contrasts are examined, unadjusted findings are more likely to include chance patterns. The registry record does not report the multiplicity strategy, so the strength of any separate secondary claim cannot be assessed with a stated adjustment plan. Secondary analyses should therefore be considered supportive and exploratory in context, rather than treated as independent confirmation of the primary result.

Numerical results for most listed secondary outcome families are not reported in the registry record. As a result, no overall conclusion about the consistency of pharmacokinetic, pharmacodynamic, safety, or immunogenicity results can be drawn from the outcome titles alone. Their inclusion describes the study’s scope, not the direction or size of findings.

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

• Efficacy: Percent Change From Baseline in Lumbar Spine Bone Mineral Density (LS-BMD) at Week 52 - Full Analysis Set (FAS)
• Efficacy: Percentage Change From Baseline (%CfB) in Lumbar Spine at Month 6 and Total Hip and Femur Neck BMD at Month 6 and Month12 - MMRM on mFAS
• Efficacy: Percentage Change From Baseline (%CfB) in Lumbar Spine BMD at Month 6 and Total Hip and Femur Neck BMD at Month 6 and 12 - ANCOVA on FAS
• Pharmacodynamics: Serum Carboxy-terminal Cross-linking Telopeptide of Type I Collagen (sCTX) Area Under the Effect Curve From Zero to 6 Months (AUEC0-6 Months) After First Dose - Modified Full Analysis Set (mFAS)
• Pharmacodynamics: %CfB Area Under the Percent Inhibition Curve From Time Zero to 6 Months (AUIC0-6 Months) in sCTX - on mFAS
• Pharmacokinetics: Maximum Observed Serum Concentration (Cmax) of Denosumab After First Dose Study Treatment (Pharmacokinetic Parameter Analysis Set)
• Pharmacokinetics: To Assess the PK Profile of MB09 Compared With EU Prolia (AUC0-6 Months) Following the First Dose
• Safety: Overall Summary of Adverse Events - Main Treatment Period - Safety Analysis Set (SAF) and Safety Analysis Set for Transition Period (SAF-TP)

9. Statistical Interpretation

10. Statistical Methods Explained

For a continuous endpoint, a group mean summarizes the average measured value or change among participants included in the analysis. The primary endpoint is reported as a least-squares mean, which is a model-based estimate rather than necessarily the arithmetic average of the observed participant values. A standard error describes the estimated uncertainty in a mean estimate. It is not the spread of individual participant outcomes; individual observations can vary more widely than the standard error suggests.

What does the repeated-measures model do?

The primary analysis used a mixed model for repeated measures (MMRM), fitted to composite percentage change in lumbar spine bone mineral density at Month 6 and Month 12. In general, repeated-measures models analyze observations from multiple timepoints together while allowing measurements from the same participant to be related. The model can estimate group contrasts across follow-up using the observed outcome records, subject to its modeling assumptions. The registry does not report the model’s full specification, including all covariates, covariance structure, or estimation details, so those features cannot be described from the record.

The primary analysis is described as using no imputation of missing data. In general, imputation fills in unobserved values with modeled or otherwise assigned values; an analysis without imputation does not insert such values into the endpoint data. That does not mean missingness is irrelevant: the amount and pattern of missing data, and assumptions about why observations are missing, can affect interpretation. Those details are not reported in the registry record.

How should the mean difference be read?

A mean difference expresses the estimated contrast between two group means, with the sign depending on which group is subtracted from which. The recalculated contrast is expressed as EU-Prolia relative to MB09; the registry analysis is reported in the reverse direction. Reversing the contrast reverses the signs of the estimate and confidence-interval limits but does not change the underlying comparison. The registry’s estimate is from a mixed-model analysis of final values, while the recalculation is a simple unadjusted re-calculation from posted summary statistics. These are related analyses, not interchangeable model specifications.

The unadjusted p-value addresses a difference-testing question under the assumptions of that recalculation. A p-value is a measure of how compatible the observed data are with a specified null hypothesis under a statistical model; it is not the probability that the null hypothesis is true. A non-significant result does not prove that groups are equivalent. Equivalence is a different inferential objective: it asks whether the plausible range of differences is contained within a prespecified acceptable interval. The registry record labels its analysis as equivalence, but the equivalence margin is not reported in the registry record.

Why do dispersion and assumptions matter?

In general, dispersion describes variation among participant measurements. More variability makes a group mean less precise when other conditions are unchanged. The posted primary summaries use standard errors, and the recalculation estimates a pooled standard deviation from those standard errors and group sizes; that pooled value is approximate. The recalculation is therefore a useful simple comparison of the posted summaries, but it does not reproduce the fitted repeated-measures model. It also does not account for model adjustments or the joint use of repeated timepoints.

Normal approximations can be useful for planning calculations, but their accuracy depends on assumptions about the outcome and sampling distribution. Over-dispersion, in general, means the data vary more than a statistical model expects. If a model understates variability, its uncertainty estimates may be too narrow; if variability is adequately represented, uncertainty estimates are more informative. The registry record does not report a diagnostic assessment of dispersion or model fit, so no trial-specific conclusion about those features is possible.

What is the role of the analysis populations?

The primary result is based on the mFAS, described as an eligible subset of the FAS with data records at each timepoint. The precise further exclusion rule in the population description is incomplete in the registry record. The secondary FAS result is based on a different named analysis population, while safety results use safety analysis sets and safety denominators. Analysis populations can differ because they apply different inclusion rules or serve different questions. Their estimates and denominators should therefore be interpreted in the context of the population named for each result.

The registry lists several outcome families and analysis methods, including MMRM and ANCOVA. In general, ANCOVA compares outcomes while adjusting for specified covariates, but the covariates used for the posted secondary analysis are not reported in the registry record. Multiple outcomes and analyses also raise multiplicity concerns: when many hypotheses are tested, unadjusted results can produce more chance findings. The multiplicity plan and any correction are not reported in the registry record, so secondary p-values or isolated findings, where available, would warrant more caution than a prespecified primary analysis.

11. Confidence Intervals and Precision

A confidence interval gives a range of values that are compatible with the observed data and the statistical model at the stated confidence level. In repeated use of the same procedure under its assumptions, intervals constructed this way would contain the target quantity at the stated rate. It is not a guarantee that a particular interval contains the true value, nor does it measure the range of individual participant outcomes.

For the recalculated primary mean difference, the estimate is -0.2 and the 95% confidence interval runs from -0.907 to 0.507. The interval includes zero, so the posted summaries are compatible with no mean difference as well as with contrasts in either direction within the interval. The interval communicates uncertainty more directly than the point estimate alone. Its width also reflects that the recalculation is based on estimated variability and group sizes, rather than on the full fitted model.

The registry’s own mixed-model estimate is 0.20, with a 95% confidence interval from -0.51 to 0.91. Its direction is reversed relative to the recalculated contrast, and its limits are rounded to fewer decimal places. The confidence intervals should be read as results from different presentations of the contrast, not as evidence of different clinical outcomes. The registry record indicates no discrepancy between them.

For an equivalence question, precision must be judged against the prespecified equivalence margin, not solely by whether an interval includes zero. A narrow interval may still fail to establish equivalence if it extends beyond the margin; a wider interval may leave substantial uncertainty. Because the margin is not reported in the registry record, the interval’s relationship to the equivalence criterion is unknown. The interval supports a description of the estimated contrast and its uncertainty, but it does not by itself confirm the registry’s equivalence conclusion.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect, not the trial’s original design calculation. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which the assumed design would have an 80% chance of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% power column uses a higher target chance of detecting that same specified effect, which requires more participants under otherwise unchanged assumptions. These percentages describe design targets for the illustration, not the probability that the trial’s result is correct.

The rows that use 100%, 75%, and 50% of the observed effect represent progressively smaller target effects. The smaller the effect to be detected, the more participants the planning calculation requires, because a smaller signal is harder to distinguish from random variation. The primary comparison’s observed effect is very small in relation to the estimated variability, so the resulting illustrative participant counts are large. They should not be treated as a proposed redesign or as evidence about the adequacy of the actual trial’s enrollment. This is not observed power; it is a forward-looking planning illustration based on the observed effect.

The planning display should be read alongside the confidence interval and the registry analysis. A planning calculation does not alter the endpoint estimate or resolve the unreported equivalence margin. Nor does it reproduce the sponsor’s repeated-measures model: it uses the stated simplified assumptions for an illustrative two-arm calculation. The registry does not report the rationale used to set the actual enrollment target, so the illustrative figures cannot establish what the original investigators planned or whether their design assumptions matched these later calculations.

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 = -0.200; pooled standard deviation σ = 3.961.
2. n = 2 × (1.96 + 0.842)² × 3.961² / -0.200² = 6,155.7, rounded up to 6,156 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 <- -0.2                      # observed difference in means
sigma <- 3.96051472956192                     # 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(5338086)
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 = 6,156 (80% power), 8,241 (90% power)
 75% of observed effect: n per arm = 10,944 (80% power), 14,651 (90% power)
 50% of observed effect: n per arm = 24,623 (80% power), 32,964 (90% power)
power.t.test: 6156.7 
Simulated power at n = 6,156 per arm: 0.797 (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’s own primary analysis is a mixed models analysis of final values and is labeled as an equivalence analysis. It reports a mean difference of 0.20, with a 95% confidence interval from -0.51 to 0.91. The simple recalculation from the posted summary statistics expresses the contrast in the opposite direction: EU-Prolia relative to MB09. It reports -0.2, with a 95% confidence interval from -0.907 to 0.507, and an unadjusted p-value of 0.579.

Because the comparison direction is reversed, the signs of the reported estimates and interval limits also reverse. The registry’s estimates and limits are rounded differently, and the registry analysis uses a fitted mixed model rather than the recalculation’s simple unadjusted approach. The registry record marks no discrepancy between the sponsor analysis and recalculation. The sponsor analysis is therefore the relevant reported analysis for the stated repeated-measures equivalence objective; the recalculation is a supplementary check based on summary statistics, not a substitute for the model or its assumptions.

The equivalence label should be read with the limitation that an equivalence margin is not reported in the registry record. The model estimate and confidence interval are available, but their relation to the criterion for equivalence cannot be verified from the record alone. The registry also does not report a p-value for this analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and multiple secondary outcomes, but a multiplicity strategy is not reported in the registry record. Multiplicity arises when researchers assess several outcomes, timepoints, contrasts, or analyses. In general, testing more hypotheses without adjustment increases the chance that at least one result will appear notable by chance. Adjustments or a prespecified hierarchy can help control that risk, but the record does not state whether such procedures were used. The recalculated p-value is unadjusted and should not be interpreted as accounting for the full set of analyses.

Missing-data handling is partly described for the primary outcome: the MMRM analysis used the composite percentage change at Month 6 and Month 12 without imputation. The record does not report how many endpoint observations were missing, why they were missing, or whether missingness differed between groups. It also does not describe sensitivity analyses for missing data. In general, a model that uses observed records still relies on assumptions about how those records relate to unobserved outcomes. Without details about missingness and sensitivity analyses, the robustness of the primary result to alternative missing-data assumptions cannot be evaluated.

The mFAS is described as an eligible subset of the FAS, with data records at each timepoint for eligible participants. The population definition is truncated after a further exclusion phrase, so that rule is not fully reported in the registry record. The primary analysis population should therefore be interpreted using the stated definition without assuming additional exclusions. The secondary result uses the FAS, and safety outcomes use safety analysis sets. Differences in populations can affect who contributes to each estimate, and their denominators should not be assumed to match.

The registry labels the primary analysis as equivalence but does not report the equivalence margin or its justification. It also does not report the original sample-size justification, interim analyses, or a detailed statistical plan. These omissions limit assessment of how the analysis was prespecified, how its error rates were controlled, and whether the achieved precision met the intended design criterion.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiac disorder (0.7%), diverticulitis (0.7%), post-acute covid-19 syndrome (0.7%), steatohepatitis (0.7%), migraine (0.7%).

For the main treatment period, the registry reports serious adverse events for 19 of 277 participants in the MB09 group and 13 of 278 participants in the EU-Prolia group. The listed counts of other adverse events are 120 of 277 and 120 of 278, respectively. These are raw counts with the reported safety denominators; they are not estimates adjusted for follow-up duration or other factors. The record reports no deaths in either main-treatment-period group.

Across the study, the reported serious adverse-event counts are 21 of 277 for MB09-MB09, 11 of 140 for EU Prolia-MB09, and 4 of 138 for EU Prolia-EU Prolia. Other adverse-event counts are also reported for these groups, as are deaths: one death in MB09-MB09 and none in the other two groups. The study-wide group labels reflect different treatment sequences, so the counts should be read using those labels rather than combined into a simple treatment comparison.

The registry lists serious-event terms including cardiac disorder, diverticulitis, post-acute COVID-19 syndrome, steatohepatitis, migraine, and thrombophlebitis, each reported at 0.7%. Counts and percentages describe reported events; they do not establish that a treatment caused an event. The record does not provide enough detail to assess event timing, exposure-adjusted rates, or causal attribution. Safety findings should be considered separately from the primary efficacy estimate.

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

The posted primary result describes a small estimated difference in average percentage change in lumbar spine bone mineral density between MB09 and EU-Prolia at Week 52, with a confidence interval that includes zero. The registry’s own analysis is labeled as an equivalence analysis and reports its model-based estimate and interval. Those results describe the measured endpoint in the analyzed population; they do not establish that every participant experienced similar changes or that the treatments are identical in every respect.

Formal equivalence is a conclusion tied to a prespecified margin: the range of differences judged acceptable for the study’s objective. Because that margin is not reported in the registry record, the estimate and confidence interval cannot be checked against the stated equivalence criterion. A non-significant difference test and an equivalence test answer different questions. The former asks whether data support a difference from zero; the latter asks whether the plausible differences are sufficiently limited under the specified margin.

The outcome is lumbar spine bone mineral density, not a direct measure of fractures, symptoms, or broader health outcomes. The record’s scope includes pharmacokinetics, pharmacodynamics, safety, and immunogenicity, but numerical information for most of those outcomes is not reported in the registry record. The efficacy result alone therefore cannot settle those other questions.

The safety counts are descriptive and use different groups and analysis periods. They do not show causation, and the registry information does not provide the detail needed to compare event rates while accounting for exposure or other factors. Likewise, planning calculations based on the observed effect are not evidence of the trial’s actual design rationale or its probability of success. The registry record supports a careful description of the posted estimates and their uncertainty, while several details needed for broader conclusions remain unreported.

18. Why This Trial Matters Statistically

This trial is statistically notable because its stated objective is equivalence, not simply detection of a difference. That distinction changes how the results should be read. A point estimate close to zero and a confidence interval spanning zero may be compatible with a small average contrast, but formal equivalence depends on whether the interval lies within a prespecified acceptable range. The registry record does not report that range. Recognizing the difference between difference-testing and equivalence-testing prevents a non-significant result from being mistaken for proof of similarity.

The analysis also illustrates why a model-based primary result and a summary-statistic recalculation answer related but distinct questions. The primary analysis uses repeated measurements and the mFAS, while the recalculation is an unadjusted estimate from posted summary statistics. Their estimates are consistent when the contrast direction and rounding are considered, but the recalculation cannot reproduce all features of the mixed model. The registry’s own analysis remains the pertinent result for the stated analysis plan.

Finally, the record demonstrates the importance of analysis populations, missing-data details, and multiplicity planning. The primary, secondary, and safety results use different populations, and the primary outcome analysis does not impute missing data. The amount and pattern of missingness, multiplicity approach, equivalence margin, and original sample-size rationale are not reported in the registry record. These details affect how confidently readers can connect the posted results to the trial’s intended claims. Statistical interpretation depends not only on the estimate, but also on the design criteria and assumptions that give the estimate meaning.

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 equivalence margin is not reported in the registry record. This is a central limitation for interpreting an equivalence analysis because the estimate and confidence interval need to be judged against that margin. The registry labels the primary analysis as equivalence, but the record does not allow readers to verify the criterion or its rationale.

The statistical plan is not fully described. The registry does not report the original sample-size justification, interim analyses, or a multiplicity strategy. It also does not provide the full MMRM specification, such as its covariance structure and covariates. These omissions limit independent evaluation of the analysis choices and the way uncertainty was handled.

The primary result uses the mFAS, whose definition is incomplete in the registry record. The record describes the population as an eligible subset of the FAS with data records at each timepoint, but the further exclusion rule is truncated. The amount, timing, and reasons for missing endpoint data are not reported, although the primary model is stated to use no imputation. Sensitivity analyses for missing data are not reported in the registry record.

Most of the listed secondary outcomes do not have numerical results available in the record for interpretation. The detailed secondary efficacy result uses a different population and method from the primary analysis. Safety results are reported as counts and denominators, without enough detail to assess exposure-adjusted rates or causal attribution. The treatment-sequence descriptions are also incomplete for the Prolia-MB09 group, limiting interpretation of that group’s dosing sequence from the registry description alone.

Finally, the recalculated comparison is a simple unadjusted analysis from posted summary statistics. It does not reproduce the sponsor’s repeated-measures model. It is useful as a consistency check, but its uncertainty interval and p-value should not be substituted for the registry’s model-based analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare Efficacy, PK, PD, Safety and IMM of MB09 to Prolia® [EU-sourced] in Postmenopausal Osteoporosis. — NCT05338086.
• Registry record last updated 2025-03-21; status last verified 2024-12.
• Results first posted 2025-03-21.
• 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

NCT05338086 is a completed randomized, double-blind, parallel, multinational phase 3 study comparing MB09 with EU-Prolia in postmenopausal women with osteoporosis. Enrollment was 558. The primary outcome was percentage change from baseline in lumbar spine bone mineral density at Week 52, analyzed in the mFAS using an MMRM without imputation of missing data.

The registry reports a sponsor mixed-model equivalence analysis and a recalculated unadjusted comparison based on posted summaries. Their estimates align after accounting for contrast direction and rounding, with no discrepancy indicated in the record. The registry does not report the equivalence margin, original sample-size justification, multiplicity strategy, or full model specification. Safety counts are reported for the main treatment period and across the study; they are descriptive and do not establish causation. Numerical results for most listed secondary outcomes are not reported in the registry record.