Clinical Trial to Assess Efficacy and Safety of the Human Anti-CD38 Antibody Felzartamab (MOR202) in IgA Nephropathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial to Assess Efficacy and Safety of the Human Anti-CD38 Antibody Felzartamab (MOR202) in IgA Nephropathy (NCT05065970), a randomized phase 2 study. The primary outcome is Part 1: Relative Change From Baseline in Urine Protein to Creatinine Ratio (UPCR) in 24-hour Urine at Month 9.

2. Clinical Question

3. Trial Design

This was a randomized, placebo-controlled, multicenter Phase IIa trial described as double blind and proof of concept, with dose evaluation. The registry lists quadruple masking and a parallel-group model. The overall enrollment was 54, and the trial status is completed. Its recorded start date was 2021-08-31 and its primary completion date was 2023-02-06.

Part 1 included placebo and three felzartamab dosing arms. The infusion schedules differed across M1, M2, and M3: the assigned drug was given on different scheduled days, with matching placebo used on specified days in M1 and M2. In M3, felzartamab was scheduled at every listed infusion visit. Part 2 was a Japan cohort, in which Japanese participants were assigned felzartamab according to body weight on the listed infusion days. The registry specifies that the primary UPCR analysis was planned for Part 1 only.

The primary outcome compared relative change from baseline in UPCR in 24-hour urine at Month 9. The stated analysis used a mixed-effects model for repeated measures, reporting least-squares means and standard errors. The full analysis set was defined as everyone randomized to Part 1, while the number analyzed for the endpoint meant the number with outcome data available. These definitions distinguish the analysis population from the number contributing data to a particular outcome.

The registry record does not report the trial’s original sample-size justification, the assumptions used to design the study, or whether interim analyses were planned or conducted. It also does not give further detail on the allocation sequence or the identity of each masked role. Those omissions limit what can be inferred about design decisions beyond the stated randomized, parallel, placebo-controlled structure.

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: A total of 54 participants diagnosed with Immunoglobulin A Nephropathy (IgAN) were enrolled in the study, of which 48 participants completed the study. The study had 2 parts - Part 1 (Global Cohort) and Part 2 (Japanese Cohort).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS) included all participants randomized to Part 1 of the study. 'Overall number of participants analyzed' signifies number of participants with data available for outcome measure analysis. The change from baseline in UPCR was planned to be analyzed in Part 1 only.

5. Baseline Characteristics

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

Population: All enrolled participants included all randomized participants from the full analysis set (FAS) plus all Japanese participants who were enrolled in Part 2. The FAS included participants randomized to Part 1 of the study.

6. Primary Endpoint

The registry lists the primary outcome as Part 1: Relative Change From Baseline in Urine Protein to Creatinine Ratio (UPCR) in 24-hour Urine at Month 9, measured over Baseline, Month 9.

The primary endpoint was relative change from baseline in UPCR measured in 24-hour urine at Month 9. UPCR relates the amount of protein in urine to creatinine and is used as a measure of proteinuria. The registry defines the reference value before treatment as the mean of measurements taken at screening and at the predose baseline visit. It states that a negative change from baseline indicates less proteinuria.

Repeated measurements can help describe how an outcome changes over time, rather than relying on a single isolated measurement. The registry says the relative change was estimated with a mixed-effects model for repeated measures and reports least-squares means with standard errors. A least-squares mean is a model-based group estimate, rather than a simple arithmetic average; the model’s role is to account for the repeated outcome measurements specified in the analysis.

UPCR is relevant to this trial because the study concerns IgA nephropathy and proteinuria is one of the measured features identified in the outcome description. The endpoint is a continuous measure, so the reported result describes average change rather than the proportion of participants crossing a response threshold. The registry lists other secondary outcomes, including additional UPCR time points, response measures, and albumin-creatinine ratio, but the primary question is specifically the Part 1 Month 9 comparison.

7. Results Posted in the Registry

• Part 1: Felzartamab Dosing Arm M1: mean -16.50 versus -24.70 on control; difference 8.20 (95% CI -45.63 to 62.03), standardized effect d = 0.13; z-test p = 0.765.
• Part 1: Felzartamab Dosing Arm M3: mean -38.50 versus -24.70 on control; difference -13.80 (95% CI -63.89 to 36.29), standardized effect d = -0.23; z-test p = 0.589.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous, and the registry reports least-squares means and standard errors from a mixed-effects model for repeated measures. This kind of model is generally used when participants have outcome measurements at more than one scheduled time. Rather than treating each time point as an unrelated result, it models the pattern of repeated observations and estimates group results within that framework. The registry identifies the model but does not report its full specification, such as all included terms, covariance structure, or the handling of every possible missing-data pattern.

What a least-squares mean represents

In general, a least-squares mean is a model-based estimate of a group average. It can differ from a raw arithmetic mean because the model may account for design features and repeated observations. For this endpoint, the registry reports least-squares means for relative change in UPCR and standard errors describing the uncertainty of those estimates. The reported group estimates are -24.7 for placebo, -16.5 for M1, -30.6 for M2, and -38.5 for M3. The outcome description states that negative change indicates less proteinuria.

A standard error summarizes the estimated sampling uncertainty of an estimate. It is not the same as the spread of individual participant values. A standard error is used to quantify how precisely the model estimates a group mean; larger uncertainty generally corresponds to a wider confidence interval. The registry gives standard errors rather than standard deviations for the primary endpoint results.

Why repeated-measures analysis is relevant

Repeated measures arise when an outcome is collected at multiple follow-up times for the same participant. Such observations are generally related because they come from the same person. A mixed-effects model for repeated measures can account for this structure while estimating changes across treatment groups and visits. In general, this approach can use available outcome measurements without reducing the analysis to only participants who have every scheduled measurement. However, the registry record does not report enough detail to determine the exact assumptions made about missing outcomes or the specific observations used at each visit.

The registry states that the primary reference UPCR value was the mean of measurements at screening and at the predose baseline visit. The endpoint then concerns relative change from that reference to Month 9, within the repeated-measures analysis. The record does not supply a full statistical analysis plan, so it does not establish all model details or explain how the endpoint’s relative-change scale was constructed beyond the description given.

Model-based ratios and simple mean differences

The sponsor-reported comparisons are geometric least-squares mean ratios from the repeated-measures model. A ratio compares model-based values on a multiplicative scale; a ratio of 1 is the no-difference reference. The reported ratios are 1.11 for M1 versus placebo, 0.92 for M2 versus placebo, and 0.82 for M3 versus placebo. Their confidence intervals are reported on that ratio scale. They are not the same quantity as an arithmetic difference between two group means.

The unadjusted recalculations use differences between the posted least-squares mean summaries. For M1 versus placebo, the recalculated mean difference is 8.2; for M3 versus placebo, it is -13.8. These comparisons use approximate pooled standard deviations derived from the arm standard errors, as indicated in the recalculation details. They do not reproduce the sponsor’s repeated-measures model, and they do not use the geometric ratio scale. As a result, the two sets of estimates answer related but not identical statistical questions.

For the recalculated comparisons, the 95% intervals extend from -45.63 to 62.03 for M1 versus placebo and from -63.89 to 36.29 for M3 versus placebo. In general, a confidence interval gives a range of estimates that are reasonably compatible with the data and the method used. An interval that includes zero for a difference is compatible with no average difference as well as effects in either direction. The wide spans indicate that the unadjusted comparisons are imprecise.

Over-dispersion and variation

In general, over-dispersion means that observed variability is greater than expected under a model’s assumed distribution. It can make standard errors too small if ignored and can therefore make intervals look more precise than they should. The primary endpoint is continuous and the reported model uses standard errors; the registry record does not identify over-dispersion as a specific concern or report a diagnostic assessment. It would be inappropriate to claim that over-dispersion occurred in these data. More generally, clinical outcome measurements can vary across participants, and small groups make it harder to estimate that variation precisely.

The recalculation estimates a pooled standard deviation approximately from the reported standard errors. That approximation is a simplifying step, not a feature of the sponsor’s model. It does not recover participant-level data, account for repeated observations, or reproduce any model adjustments that may have been made. This distinction matters when interpreting both the estimates and the confidence intervals.

The registry also lists three sponsor-reported superiority comparisons, one for each felzartamab dosing arm against placebo. The record does not state whether or how these comparisons were adjusted for multiplicity. When several comparisons are examined, the chance of at least one apparently notable result can increase in general; adjustment methods can address that issue, but the record does not identify a method. The reported estimates should therefore be read with the analysis plan details that are available, while recognizing that the multiplicity approach is not reported in the registry record.

10. Confidence Intervals and Precision

The sponsor-reported 95% confidence intervals are wide relative to the central estimates. M1 versus placebo has a geometric least-squares mean ratio of 1.11, with a confidence interval from 0.67 to 1.84. M2 versus placebo has a ratio of 0.92, with an interval from 0.54 to 1.57. M3 versus placebo has a ratio of 0.82, with an interval from 0.49 to 1.35. Each interval includes 1, the no-difference reference for a ratio. Thus, the reported comparisons do not identify a narrow range of plausible ratios.

The unadjusted recalculated intervals also span zero. The M1-minus-placebo estimate is 8.2, with an interval from -45.63 to 62.03; the M3-minus-placebo estimate is -13.8, with an interval from -63.89 to 36.29. These ranges allow for differences in either direction and are wide, so the point estimates alone should not be read as precise estimates of the group contrasts. The recalculation does not include a comparison for M2.

Confidence intervals are statistical ranges that express uncertainty under the analysis method; they are not guarantees that a particular value is the true effect. Their width reflects both the observed variability and the amount of information available. The endpoint analysis groups were small: the registry lists 11 participants for placebo, 11 for M1, 9 for M2, and 12 for M3. The intervals should be interpreted in light of those group sizes and the model used.

For the sponsor-reported ratio comparisons, the absence of a narrow interval means the data are compatible with a range of relative effects. For the recalculated differences, including zero means that the data do not resolve the direction of the simple mean contrast. Neither result demonstrates equivalence. Equivalence requires a prespecified margin and an analysis designed to assess whether the effect lies within that margin; such a margin is not reported in the registry record.

11. 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 illustrations based on the observed effect, not the trial’s original design assumptions. For M1 versus placebo, planning for 100% of the observed effect gives 969 participants per arm for 80% power and 1,297 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,722 participants per arm for 80% power and 2,305 participants per arm for 90% power. Planning for 50% of the observed effect gives 3,875 participants per arm for 80% power and 5,187 participants per arm for 90% power.

For M3 versus placebo, planning for 100% of the observed effect gives 306 participants per arm for 80% power and 410 participants per arm for 90% power. Planning for 75% of the observed effect gives 544 participants per arm for 80% power and 728 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,224 participants per arm for 80% power and 1,638 participants per arm for 90% power. These figures are participants per arm, not total events.

In general, 80% power means an 80% chance of detecting an effect of the assumed size under the planning assumptions if that effect is present; 90% power represents a higher target chance under the same general framework. The calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Smaller effects require more participants to detect than larger effects, which is why the displayed values rise when planning for a smaller fraction of the observed effect. These figures are not observed power. The registry record does not report the original trial’s sample-size justification or its design assumptions.

12. 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 = 8.200; pooled standard deviation σ = 64.409.
2. n = 2 × (1.96 + 0.842)² × 64.409² / 8.200² = 968.5, rounded up to 969 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 <- 8.2                      # observed difference in means
sigma <- 64.4088619679                     # 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(5065970)
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 = 969 (80% power), 1,297 (90% power)
 75% of observed effect: n per arm = 1,722 (80% power), 2,305 (90% power)
 50% of observed effect: n per arm = 3,875 (80% power), 5,187 (90% power)
power.t.test: 969.5 
Simulated power at n = 969 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.

13. Analyses Reported by the Sponsor

The sponsor’s own primary comparisons use a mixed-effects model for repeated measures and report geometric least-squares mean ratios: 1.11 for M1 versus placebo, 0.92 for M2 versus placebo, and 0.82 for M3 versus placebo. Each has a 95% confidence interval that includes 1. The p-values are reported in the registry, but are not repeated because their displayed precision exceeds three decimal places.

The supplementary recalculations are simple unadjusted mean differences derived from the posted summary statistics. They give 8.2 for M1 versus placebo and -13.8 for M3 versus placebo, with intervals that include zero. No recalculated comparison is listed for M2. These estimates are on a difference scale, while the sponsor results use a ratio scale, and the calculations do not reproduce the repeated-measures model. They should therefore be treated as a separate, approximate view of the posted summaries, not as a substitute for the trial’s reported analysis. No discrepancy is flagged between the sponsor analysis and the recalculation; the sponsor’s analysis remains the trial’s own reported result.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists three sponsor-reported comparisons of a felzartamab dosing arm with placebo for the primary endpoint. It does not report whether the statistical testing accounted for making multiple comparisons, or what adjustment method was used. This matters because testing several comparisons can affect how individual p-values and confidence intervals should be interpreted. The absence of a reported method does not establish that no adjustment was used; it means that the approach is not reported in the registry record.

The registry describes the full analysis set as all participants randomized to Part 1 and defines the number analyzed for an outcome as the number with data available for that analysis. It reports primary endpoint data for 11 participants in placebo, 11 in M1, 9 in M2, and 12 in M3. The record does not explain why these numbers differ across groups or describe missing outcome data, including its amount, timing, or handling in the model. The model is identified as mixed effects for repeated measures, but the assumptions about missingness and the exact implementation are not reported.

The registry lists 13 outcome measures and 12 secondary outcomes posted. Those outcomes include additional UPCR measurements at later months, complete response, response, albumin-creatinine ratio, duration and time to response, and integrative analyses of immunoglobulin A concentration and infusion-related reactions. It reports three analyses for the primary result. The record does not provide enough information to determine how the full family of primary and secondary outcomes was prioritized or how multiplicity across outcomes was handled.

The randomized Part 1 analysis population is distinct from the safety groups, which include the Japan cohort as a separate group. The registry record does not provide a participant flow account or detailed analysis-population counts for every outcome. These omissions make it difficult to assess the full impact of missing measurements and analysis choices on the estimates.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infusion related reaction (9.1%), tendon rupture (8.3%), dedifferentiated liposarcoma (8.3%).

The safety record reports serious adverse events and other adverse events by study group. For placebo, 1 of 12 participants at risk had a serious adverse event and 9 of 12 had an other adverse event. In M1, the corresponding counts were 1 of 12 and 11 of 12. In M2, they were 1 of 11 and 9 of 11. In M3, no serious adverse events were reported among 13 participants at risk, while 12 of 13 had an other adverse event. In the Japan cohort, no serious adverse events were reported among 6 participants at risk, and 6 of 6 had an other adverse event. No deaths were reported in any group.

These are participant counts, not event counts, and the record does not give enough detail to establish whether participants experienced more than one event or how events were distributed over time. It also does not specify a common observation period for these group summaries. The listed serious-event terms include infusion related reaction at 9.1%, tendon rupture at 8.3%, and dedifferentiated liposarcoma at 8.3%; the registry excerpt does not identify a group attribution for these term percentages. Safety counts describe the posted observations and should not be treated as a comparative risk analysis.

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

The primary outcome describes relative change in UPCR from baseline to Month 9 in Part 1. Negative values indicate less proteinuria according to the registry’s endpoint definition. The model-based estimates were negative in all four groups: -24.7 for placebo, -16.5 for M1, -30.6 for M2, and -38.5 for M3. The estimates are group-level results and do not show how individual participants changed.

The sponsor-reported ratios and their confidence intervals do not precisely distinguish the dosing arms from placebo. Every reported interval includes the ratio reference value of 1. The supplementary unadjusted comparisons likewise have confidence intervals that include zero. Those results reflect uncertainty, and they do not establish that the groups are equivalent or that a clinically meaningful difference is absent. The registry record does not state a clinical importance threshold for this endpoint.

These statistics do not establish that felzartamab works or does not work. They describe the trial’s posted endpoint estimates and the precision with which group contrasts were estimated. The relatively small endpoint analysis groups and broad intervals mean that a range of effects remains compatible with the results. A point estimate should not be read as a settled treatment effect, particularly when the corresponding interval spans values on either side of the no-difference reference.

The primary analysis was planned for Part 1, and the findings should not be extended to the separate Japan cohort based on these primary results. Nor should the Month 9 endpoint be treated as a complete account of longer-term outcomes: secondary outcomes included additional time points, but their results are not described in the primary endpoint statistics. The registry record also does not provide a full statistical analysis plan, detailed missing-data information, or the trial’s original sample-size rationale. These limits constrain interpretation without changing what the posted estimates themselves report.

17. Why This Trial Matters Statistically

This trial illustrates several important statistical distinctions in clinical research. First, a group’s change from baseline is not the same as a randomized comparison between groups. The placebo and felzartamab arms all had negative model-based mean changes, but the question of interest is whether the groups differ, not whether one group’s estimate is below zero on its own.

Second, the reported analysis and a summary-statistic recalculation can target different quantities. The sponsor used a repeated-measures model and reported geometric least-squares mean ratios. The unadjusted recalculations compare group summaries using mean differences and approximate pooled variability. Those estimates are complementary descriptions, not duplicate analyses. Their scales, assumptions, and use of the available information differ.

Third, uncertainty is central to interpretation. The sponsor’s confidence intervals span the no-difference ratio reference, and the recalculated difference intervals span zero. These wide intervals show why point estimates alone cannot support a confident ranking of dosing schedules. The small outcome analysis groups limit the precision available from this trial.

Finally, design transparency matters. The registry identifies the repeated-measures model and the analysis population, but does not report the original sample-size justification, model details, multiplicity approach, or missing-data handling. Without those details, readers can interpret the posted statistics and their uncertainty, but cannot fully reconstruct every analytic decision. The distinction between an exploratory Phase IIa proof-of-concept study and a definitive estimate is also relevant to how much certainty these results can support.

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 endpoint analysis involved small groups, with 9 to 12 participants contributing data in each Part 1 arm. Confidence intervals for the group contrasts are broad, leaving substantial uncertainty about the magnitude and direction of differences. The registry reports overall enrollment of 54, but the primary endpoint was planned for Part 1 only, and the outcome-specific analysis counts are smaller than the overall enrollment.

The registry record does not report the trial’s original sample-size rationale, so the adequacy of the planned sample size for the primary endpoint cannot be assessed from this record. It also does not report the detailed repeated-measures model specification, handling of missing observations, or multiplicity strategy for the reported comparisons. The primary outcome description states that participants with available data were analyzed, but does not provide detailed missing-data counts or reasons.

The unadjusted recalculations are limited to M1 and M3 versus placebo. They use approximate pooled standard deviations derived from arm standard errors and do not reproduce the sponsor’s repeated-measures model. There is no recalculated M2 contrast. Their intervals should be interpreted as approximate, unadjusted comparisons rather than as replacements for the registry’s model-based results.

The registry lists additional secondary outcomes, but the primary endpoint statistics do not describe their results. The safety record gives participant counts by group but does not report event timing or clearly attribute the listed serious-event term percentages to a group. The primary results concern Part 1 and do not establish results for the separate Japan cohort. These limitations restrict the scope and precision of conclusions that can be drawn from the posted record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Trial to Assess Efficacy and Safety of the Human Anti-CD38 Antibody Felzartamab (MOR202) in IgA Nephropathy — NCT05065970.
• Registry record last updated 2026-04-28; status last verified 2026-04.
• Results first posted 2026-04-28.
• 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

NCT05065970 was a completed, randomized, placebo-controlled, multicenter Phase IIa trial of felzartamab in IgA nephropathy, with overall enrollment of 54. The primary outcome was relative change from baseline in UPCR in 24-hour urine at Month 9, analyzed in Part 1 using a mixed-effects model for repeated measures.

The registry reports least-squares mean changes for placebo and three dosing arms, plus geometric least-squares mean ratios for each dosing arm versus placebo. The reported 95% confidence intervals include 1, while unadjusted recalculated mean-difference intervals include zero. The estimates are imprecise, and the trial record does not report key details including the original sample-size rationale, multiplicity handling, and missing-data approach.