Comparison of Efficacy, Pharmacodynamics, Safety, and Immunogenicity Between Bmab 1000 and Prolia® in Postmenopausal Women With Osteoporosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Efficacy, Pharmacodynamics, Safety, and Immunogenicity Between Bmab 1000 and Prolia® in Postmenopausal Women With Osteoporosis (NCT05345691), a randomized phase 3 study. The primary outcome is Percentage Change in Lumbar Spine BMD (Bone Mineral Density).

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, multicenter, parallel-arm Phase 3 study comparing Bmab 1000 with Prolia® in postmenopausal women with osteoporosis. Participants were assigned to one of the two biological interventions. Randomization helps limit systematic differences between groups at study entry, while double masking is intended to limit the influence of treatment knowledge on participants’ experience and study assessments. The registry record does not describe the randomization procedure or masking details.

The registry reports enrollment of 479. For the primary endpoint, the full analysis set is named as the population of interest. The endpoint was percentage change from baseline in lumbar spine bone mineral density at Week 52. The primary comparison is described as a test of equivalent efficacy, but the equivalence margin and the formal sponsor analysis are not reported in the registry record.

The study began on 2022-05-24, reached primary completion on 2024-06-12, and is listed as completed. Its planned scope included pharmacokinetic, pharmacodynamic, safety, and immunogenicity assessments as well as efficacy. Secondary outcomes include bone resorption and formation markers, lumbar spine and total hip bone mineral density, treatment-emergent adverse events, anti-drug antibodies, and neutralizing antibodies. The registry lists 18 outcome measures, while posted secondary results cover 17.

The reported arm summaries and recalculated comparisons should be distinguished from a full account of the trial’s statistical analysis. The registry record does not report a detailed statistical analysis plan, the original sample-size assumptions, or the sponsor’s formal inferential analysis for the primary equivalence question.

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.

Part 1

Part 2

Analysis population for the primary outcome, as defined in the registry: Full analysis set

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage Change in Lumbar Spine BMD (Bone Mineral Density), measured over Baseline and Week 52.

The primary endpoint is percentage change in lumbar spine bone mineral density from baseline to Week 52. Bone mineral density, or BMD, measures the amount of mineral in bone. Expressing the endpoint as percentage change puts the follow-up measurement in relation to baseline, allowing the comparison to focus on change over the study period rather than only on the endpoint value.

Lumbar spine BMD is used as an efficacy measure in this trial because the study’s stated primary question concerns whether the two treatments have equivalent effects on this continuous measure. The registry lists the primary summary as a least-squares mean with a standard error, in the full analysis set. A least-squares mean is an estimated group mean from a statistical model; however, the model details are not reported in the registry record. The standard error describes the uncertainty in that estimated mean, rather than the spread of individual participants’ BMD changes.

The Week 52 focus is important: a result at that time point addresses the registered primary question, while earlier measurements and other outcomes address separate questions. A close estimated difference does not by itself demonstrate equivalence. Formal interpretation depends on a prespecified equivalence margin and an appropriate analysis. The margin and the sponsor’s formal equivalence conclusion are not reported in the registry record.

7. Results Posted in the Registry

• Prolia®: mean 1.44 versus 1.70 on control; difference -0.26 (95% CI -1.67 to 1.16), standardized effect d = -0.03; z-test p = 0.721.

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.

AUEC (Area Under the Effect Curve) of the Bone Resorption Marker sCTX (Serum C-terminal Telopeptide of Type 1 Collagen)

• 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:
  • Prolia®:: mean 123.00 versus 127.00 on control; difference -4.00 (95% CI -20.98 to 12.98), standardized effect d = -0.05; z-test p = 0.644.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prolia®: and the control. The interval gives the range of effects that remain compatible with the data.

Percentage Change in Lumbar Spine BMD

• 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:
  • Prolia®:: mean 3.70 versus 3.87 on control; difference -0.17 (95% CI -2.36 to 2.01), standardized effect d = -0.01; z-test p = 0.877.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prolia®: and the control. The interval gives the range of effects that remain compatible with the data.

Percentage Change in Total Hip BMD by DXA (Dual-energy X-ray Absorptiometry)

• 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:
  • Prolia®:: mean 1.44 versus 1.70 on control; difference -0.26 (95% CI -1.67 to 1.16), standardized effect d = -0.03; z-test p = 0.721.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prolia®: and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the evidence beyond the primary Week 52 lumbar spine BMD question. They include a bone resorption marker, lumbar spine and total hip BMD at other time points, a bone formation marker, treatment-emergent adverse events, and measures of immune response. Together, these outcomes address related but distinct aspects of pharmacodynamics, bone response, safety, and immunogenicity.

The posted continuous-outcome summaries generally show similar group estimates, with recalculated intervals that include zero. This pattern is compatible with no clear difference in the reported comparisons, but it does not establish equivalence across those outcomes. Each endpoint has its own measure, time frame, uncertainty, and analysis considerations. The secondary estimates should not be treated as independent confirmation of the primary result or as a substitute for the primary Week 52 equivalence analysis.

The registry record lists 17 posted secondary outcomes and 18 outcome measures overall. It does not report secondary analyses in its reported-analysis list. Unadjusted comparisons across multiple outcomes carry less weight because testing many endpoints can increase the chance of apparently notable findings arising by chance. The registry record does not state whether multiplicity was addressed, or whether particular secondary endpoints were designated as confirmatory.

Accordingly, the secondary results are best read as descriptive context for the primary comparison and as a record of the measured domains. They can indicate whether observed patterns are broadly similar across measures, but they do not independently settle whether the treatments are equivalent, nor do they establish differences in outcomes where the uncertainty remains substantial.

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

• AUEC (Area Under the Effect Curve) of the Bone Resorption Marker sCTX (Serum C-terminal Telopeptide of Type 1 Collagen)
• Percentage Change in Lumbar Spine BMD
• Percentage Change in Total Hip BMD by DXA (Dual-energy X-ray Absorptiometry)
• Serum Concentrations of P1NP (Procollagen Type 1 N-terminal Propeptide)
• Incidence of TEAEs (Treatment-emergent Adverse Events) up to 6 Months After the Second Dose
• Incidence of ADA (Anti-drug Antibody)
• Incidence of ADA (Anti-drug Antibody)
• Incidence of NAb (Neutralizing Antibody) up to Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a percentage change in lumbar spine BMD. The registry summarizes it using least-squares means and standard errors. A mean describes the central value of a continuous measurement. A least-squares mean is generally a model-based estimate rather than a simple arithmetic average; the exact model and any adjustment variables are not reported in the registry record. A standard error describes the uncertainty in an estimated mean. It is not the same as a standard deviation, which describes variation among individual measurements.

What does a mean difference represent?

The comparison is expressed as the Prolia® estimate relative to the Bmab 1000 estimate. A negative difference indicates that the posted estimate for Prolia® is lower than the posted estimate for Bmab 1000 under that direction of comparison. The primary recalculated mean difference is -0.258. This is a difference in percentage-change units, not a relative percentage or a ratio. The comparison does not adjust for factors unless those are specified in the analysis; model details are not reported in the registry record.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the data under the method used to calculate it. It communicates uncertainty around the estimated difference, rather than presenting the point estimate as exact. The primary interval is -1.672 to 1.156. Because it includes zero, the recalculated comparison does not clearly distinguish a positive difference from a negative one. For an equivalence objective, the key question is not simply whether zero is included. The interval must be interpreted against the prespecified equivalence margin, which is not reported in the registry record.

How should the p-value be read?

The recalculated unadjusted p-value is 0.721. In general, a p-value measures 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. Here it is an unadjusted recalculation from posted summary statistics, not a reported sponsor analysis. It does not establish equivalence, and it does not express the size or clinical importance of a difference.

What is the role of standardized effects?

A standardized effect expresses a difference relative to a measure of variability, which can help compare effects measured on different scales. The posted primary standardized effect is -0.033. Standardization does not replace interpretation in the endpoint’s original units, and it cannot determine whether a difference is clinically acceptable. The pooled standard deviation is approximate in the primary comparison, as indicated in the posted calculations. That approximation is a reason to treat the standardized summary as a descriptive aid rather than as a formal trial conclusion.

Why can planning illustrations be very large?

Sample-size planning depends on the effect a future study aims to detect, the variability of the outcome, the chosen significance level, allocation, and statistical method. When the assumed target effect is smaller, a study generally needs more participants to distinguish it from random variation. The planning illustrations use fractions of the observed effect and stated assumptions; they are not evidence about the power of this completed trial. The original design assumptions for the trial are not reported in the registry record.

Why are analyses of secondary outcomes less definitive?

Secondary outcomes address additional questions, often using different measures or time points. Testing many outcomes increases the chance that some results appear notable by chance. Methods such as prespecified testing sequences or multiplicity adjustments can address this issue, but the registry record does not report whether or how these methods were used. The secondary recalculations are unadjusted and should be treated as exploratory descriptions, not as a set of independent confirmatory findings.

Several posted summaries report standard deviations, while the BMD summaries report standard errors for least-squares means. These quantities answer different questions and should not be compared as if they were the same kind of spread. In general, over-dispersion means that outcomes vary more than a statistical model assumes. If that occurs and is not accounted for, uncertainty estimates can be too small and inferential conclusions too confident. The registry record does not report whether over-dispersion was assessed or relevant to these analyses.

11. Confidence Intervals and Precision

The primary recalculated mean difference is -0.258, with a 95% confidence interval from -1.672 to 1.156. The interval is the central guide to precision: it shows that the estimate is uncertain and remains compatible with differences in either direction. The point estimate alone should not be treated as an exact treatment contrast.

A confidence interval is a range generated by a statistical procedure that, under its assumptions, would contain the true parameter at its stated coverage level in repeated use. It is not a probability statement about the particular interval after it has been calculated. The interval’s width reflects sampling uncertainty as well as the method and assumptions used to estimate it. The registry record does not report the full model or the formal sponsor analysis, so the recalculated interval should be read as an unadjusted summary-statistic calculation.

For an equivalence question, precision has a specific interpretation. The interval needs to fall within a prespecified range around zero, defined by an equivalence margin. The registry record does not report that margin. Consequently, the interval cannot be used to decide whether the uncertainty is sufficiently narrow for equivalence, even though the group estimates are close.

The standard errors accompanying the least-squares means describe uncertainty in each estimated mean, not the variation between individual participants. The confidence interval for the difference is more directly relevant to the treatment comparison. Without the equivalence margin, a definitive clinical threshold, or details of the sponsor’s analysis, the registry summaries support a description of uncertainty but not a formal 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 sample-size illustrations use participants per arm for 80% power and participants per arm for 90% power. They are not total-event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect. The original trial’s own design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is present and the model assumptions hold. The 90% power column describes the corresponding target at a higher chance of detection. These are planning targets, not guarantees: actual performance depends on the true effect, variability, missing data, and whether the planning assumptions are appropriate.

The rows vary the target from 100% of the observed effect to 75% and 50% of the observed effect. Smaller effects need more participants to distinguish them from random variation, so the illustrative requirements rise as the assumed effect gets smaller. The calculations are based on the observed effect and are planning illustrations, not observed power for the completed study. They do not show whether the original trial was adequately powered for its prespecified equivalence objective, particularly because its original assumptions and equivalence margin are not reported.

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 = -0.258; pooled standard deviation σ = 7.838.
2. n = 2 × (1.96 + 0.842)² × 7.838² / -0.258² = 14,488.4, rounded up to 14,489 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 <- -0.258                      # observed difference in means
sigma <- 7.83810682810099                     # 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(5345691)
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 = 14,489 (80% power), 19,396 (90% power)
 75% of observed effect: n per arm = 25,758 (80% power), 34,482 (90% power)
 50% of observed effect: n per arm = 57,954 (80% power), 77,584 (90% power)
power.t.test: 14489.4 
Simulated power at n = 14,489 per arm: 0.802 (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 registry identifies a primary endpoint and several secondary outcomes, but the record does not report a detailed statistical analysis plan. It also does not report whether tests across the secondary endpoints were adjusted for multiplicity, whether a testing hierarchy was used, or which secondary outcomes were intended to support confirmatory claims.

Multiplicity matters when several hypotheses are tested. In general, the more tests conducted, the greater the chance that at least one result will appear statistically notable by chance, even if there is no true effect. Prespecified strategies can control this risk, for example by adjusting significance thresholds or by setting an order for testing. Without the plan and adjustment details, unadjusted secondary p-values should be interpreted cautiously and should not be treated as a collection of definitive findings.

The registry names the full analysis set for the primary endpoint, but does not define it in detail. The record does not report the analysis population used for each secondary endpoint, how missing data or withdrawals were handled, whether any imputation was used, or whether sensitivity analyses assessed the influence of missing observations. These details matter because estimates can depend on which participants and measurements enter an analysis and on the assumptions made about unavailable outcomes.

The primary objective is described as demonstrating equivalent efficacy, but the equivalence margin, the formal statistical method, and the sponsor’s analysis result are not reported in the registry record. Equivalence requires a prespecified acceptable range and an analysis that evaluates the treatment difference against that range. The posted recalculations do not fill those gaps. They offer an unadjusted view of the summary statistics, not a reconstruction of the complete 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: invasive lobular breast carcinoma (1.0%), atrial fibrillation (1.0%), dizziness (0.9%), abdominal pain (0.5%), gastric ulcer (0.5%).

The registry reports serious adverse event counts with the number at risk for each arm. For Bmab 1000, 15 serious adverse events are reported among 218 at risk; for Prolia®, 2 are reported among 104 at risk. These are counts and denominators as recorded. The record also reports 0 deaths for Bmab 1000 and 1 for Prolia®.

These figures describe the safety data recorded during the trial; they do not by themselves establish that an intervention caused an event. The registry record does not provide enough detail in these summaries to assess differences in exposure time, event timing, participant characteristics, or the formal method used to compare safety between groups. The at-risk numbers should not be assumed to match the enrollment count or the primary analysis population.

The listed serious-event terms include invasive lobular breast carcinoma, atrial fibrillation, dizziness, abdominal pain, gastric ulcer, and inflammatory bowel disease, with the percentages recorded for those terms. The registry record does not provide additional context in this summary to determine causality or clinical interpretation. These figures should be read as reported safety events, not as evidence that a treatment caused or prevented any particular event.

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

The posted primary summaries describe close mean percentage changes in lumbar spine BMD for Bmab 1000 and Prolia® at Week 52. The recalculated difference is -0.258, and its 95% confidence interval ranges from -1.672 to 1.156. This interval includes zero, so the recalculation does not clearly show a difference between the group estimates.

That finding does not prove that the treatments are identical, and it does not establish equivalence. Equivalence is a specific statistical claim: the uncertainty around the difference must be narrow enough to fit inside a prespecified acceptable range. The registry record does not report that range or the sponsor’s formal analysis. A non-significant unadjusted comparison cannot substitute for those requirements.

The results also should not be interpreted as a complete account of treatment benefit or risk. The endpoint addresses one measure of bone mineral density at a particular time point. Secondary outcomes cover additional efficacy, pharmacodynamic, safety, and immunogenicity measures, but their unadjusted results have limitations and do not resolve the primary equivalence question. Serious adverse event counts are descriptive and do not by themselves establish causation or a comparative safety conclusion.

The most defensible reading is therefore limited: the posted summaries show similar observed primary means, with uncertainty that spans differences in either direction. Whether that uncertainty satisfies the trial’s equivalence objective cannot be determined from the registry record because the equivalence margin and formal sponsor analysis are not reported. The summaries do not establish that either intervention is superior, inferior, equivalent, or safer.

17. Why This Trial Matters Statistically

This trial illustrates why the statistical question must match the study objective. The registered primary objective is equivalence, but a comparison that merely fails to show a difference is not an equivalence test. Equivalence requires an acceptable margin set in advance and an interval sufficiently contained within that margin. The registry record does not report the margin or the sponsor’s formal analysis, so the posted group summaries cannot answer the full primary question.

It also illustrates the importance of distinguishing estimates from uncertainty. The primary group means are close, while the recalculated confidence interval spans values on either side of zero. Reading only the point estimates would understate the uncertainty; reading only the unadjusted p-value would not address whether the interval is narrow enough for equivalence.

The registry record contains a broad set of secondary outcomes, including bone measures, safety events, and immunogenicity. That breadth can help describe multiple aspects of a trial, but it also raises questions about multiplicity, missing data, and which outcomes were confirmatory. Those methods are not reported in the registry record, so the secondary results should be understood as supportive description rather than a replacement for the primary analysis.

Finally, planning illustrations based on observed effects are not evidence of the trial’s original design adequacy or its observed power. The original sample-size rationale is not reported. Clear separation of trial planning, posted summaries, and formal inferential conclusions is essential for interpreting registry results responsibly.

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 registry record does not report the equivalence margin or the sponsor’s formal analysis of the primary endpoint. This is a central limitation because the registered question is whether the treatments have equivalent efficacy. The recalculated unadjusted difference and interval are not sufficient to establish that claim without the prespecified margin and confirmatory analysis.

The statistical model behind the least-squares means is not reported. The record also does not describe adjustment variables, the detailed definition of the full analysis set, the handling of missing measurements, or sensitivity analyses. These omissions limit assessment of whether the recalculation aligns with the planned analysis and how robust the result is to analytic choices.

The registry reports enrollment of 479, but the arm-level numbers associated with outcome summaries and safety outcomes vary. The record does not explain all differences in denominators or provide enough detail to infer why participants or measurements are not represented in each summary. Those numbers should therefore be interpreted within their reported outcome context rather than assumed to describe the same analysis population.

The secondary outcomes are numerous, and the registry does not report whether multiplicity was addressed. Their unadjusted comparisons are less conclusive as a group, and the record lists 17 posted secondary outcomes while reporting 18 outcome measures overall. The original sample-size assumptions, detailed dosing information in the arm descriptions, and reasons for missing outcome data are also not reported. These limitations constrain interpretation without establishing that any particular result is biased or invalid.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Efficacy, Pharmacodynamics, Safety, and Immunogenicity Between Bmab 1000 and Prolia® in Postmenopausal Women With Osteoporosis — NCT05345691.
• Registry record last updated 2025-09-09; status last verified 2025-08.
• Results first posted 2025-08-19.
• 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 record describes a completed randomized, double-blind, multicenter, parallel-arm Phase 3 study of Bmab 1000 versus Prolia® in postmenopausal women with osteoporosis. Enrollment was 479. The primary endpoint was percentage change in lumbar spine BMD from baseline to Week 52 in the full analysis set, with the stated objective of demonstrating equivalent efficacy.

The posted primary least-squares means were 1.698 for Bmab 1000 and 1.44 for Prolia®. The recalculated unadjusted difference was -0.258, with a 95% confidence interval from -1.672 to 1.156 and an unadjusted p-value of 0.721. These calculations do not establish equivalence; the equivalence margin and sponsor’s formal analysis are not reported in the registry record.

The registry also lists secondary bone, safety, and immunogenicity outcomes. Its record does not report the detailed analysis plan, multiplicity procedures, or handling of missing data.