Daratumumab Retreatment in Participants With Multiple Myeloma Who Have Been Previously Treated With Daratumumab: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Daratumumab Retreatment in Participants With Multiple Myeloma Who Have Been Previously Treated With Daratumumab (NCT03871829), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving Very Good Partial Response (VGPR) or Better Response.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, parallel-group study with no masking recorded. Its stated purpose was to evaluate daratumumab retreatment by comparing daratumumab subcutaneous administration with carfilzomib and dexamethasone against carfilzomib and dexamethasone alone. The registry lists 88 participants enrolled. The study status is terminated. The reason for termination is not reported in the registry record, so the status alone does not establish why the trial ended or how termination affected the analyses.

Participants were assigned to one of two groups. Arm A received carfilzomib and dexamethasone, and Arm B received daratumumab subcutaneous in combination with carfilzomib and dexamethasone. Randomization supports a comparison between assigned groups, but the registry record does not report the allocation ratio, randomization procedure, or any stratification factors. Masking is listed as none, so this was an open-label comparison. The potential relevance of knowing treatment assignment is, especially for an endpoint based on response assessment.

The primary outcome was the percentage achieving very good partial response or better. The registry gives a response-evaluable analysis population of participants with confirmed disease and measurable disease at baseline or screening, rather than describing the primary result as an analysis of every enrolled participant. The posted arm denominators are 39 and 41. The safety results use a different denominator, 43 participants at risk in each arm, as shown in the adverse-event section. The reason these analysis sets differ is not reported in the registry record.

The registry also lists secondary outcomes, including overall response rate, complete response or better, progression-free survival, overall survival, minimal residual disease, time to next treatment, serum daratumumab concentrations, and anti-recombinant human hyaluronidase antibodies. Statistical analysis entries are not posted. Details of the original design assumptions, treatment discontinuation, and analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The response-evaluable analysis set included participants who had confirmed diagnosis of multiple myeloma and measurable disease at baseline or screening visit.

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 of Participants Achieving Very Good Partial Response (VGPR) or Better Response, measured over Up to 3 years and 4 months.

The primary endpoint is the percentage of participants achieving very good partial response or better as their best response. The registry defines this category to include very good partial response, complete response, or stringent complete response under International Myeloma Working Group criteria. The response had to occur during or after study treatment and before the start of subsequent anti-myeloma therapy. The registry gives a timeframe of up to 3 years and 4 months.

A response endpoint summarizes whether participants met specified disease-response criteria during the assessment period. It is different from an endpoint such as overall survival, which concerns time to death, or progression-free survival, which concerns time to progression or death. Response can therefore describe an aspect of disease control without itself answering how long participants lived or remained progression-free. Those time-to-event outcomes are listed among the secondary outcomes, but their results are not included in the posted summary.

Response rates are useful for comparing the proportions meeting a defined response threshold in each group. The choice of threshold matters: very good partial response or better is a composite category, while the separately listed complete-response endpoint uses a stricter response level. The endpoint description specifies the response-evaluable population and the point at which subsequent therapy ends the response window. How missing assessments or participants without an evaluable response were handled is not reported in the registry record.

7. Results Posted in the Registry

• Arm B: Dara-SC in Combination With Kd (DKd): 48.8% (20/41) versus 46.2% (18/39) on control; risk difference 2.6 percentage points (95% CI -19.3 to 24.5), risk ratio 1.06 (0.67–1.68); unadjusted two-proportion z-test p = 0.814.

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.

Overall Response Rate (ORR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Dara-SC in Combination With Kd (DKd): 75.6% (31/41) versus 64.1% (25/39) on control; risk difference 11.5 percentage points (95% CI -8.5 to 31.5), risk ratio 1.18 (0.88–1.58); unadjusted two-proportion z-test p = 0.262.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Dara-SC in Combination With Kd (DKd) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving Complete Response (CR) or Better

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Dara-SC in Combination With Kd (DKd): 12.2% (5/41) versus 25.6% (10/39) on control; risk difference -13.4 percentage points (95% CI -30.4 to 3.5), risk ratio 0.48 (0.18–1.27); unadjusted two-proportion z-test p = 0.124.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Dara-SC in Combination With Kd (DKd) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Negative Minimal Residual Disease (MRD)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Dara-SC in Combination With Kd (DKd): 6.8% (3/44) versus 11.4% (5/44) on control; risk difference -4.5 percentage points (95% CI -16.5 to 7.4), risk ratio 0.60 (0.15–2.36); unadjusted two-proportion z-test p = 0.458.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Dara-SC in Combination With Kd (DKd) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results add context to the primary response endpoint, but they do not provide a single uniform pattern across all measures. The posted summaries include overall response rate, complete response or better, and negative minimal residual disease. The displayed estimates move in different directions across these response measures, and their intervals are broad. This variation is a reason to avoid treating any one secondary point estimate as a definitive account of the treatment comparison.

These measures are related but not interchangeable. Overall response rate uses a broader response category than the primary endpoint; complete response or better applies a stricter threshold; and negative minimal residual disease is a distinct assessment. A pattern across them can help describe the response data, but agreement or disagreement among measures does not automatically confirm or refute the primary result. They also do not replace the separately listed time-to-event outcomes, such as progression-free survival and overall survival. Their posted results are not included in the quantitative summaries.

The secondary findings should carry less weight than a prespecified primary analysis, particularly because the registry lists no analysis entries and does not report a multiplicity plan. When many outcomes are examined, some may appear notable by chance even when there is no underlying effect. Adjusting for multiple comparisons is one general approach to controlling the chance of false-positive findings across a family of tests, but whether any adjustment was planned or used is not reported in the registry record. The secondary comparisons shown are unadjusted in the posted summaries.

Accordingly, the secondary endpoints are best treated as descriptive and hypothesis-generating in this record. They help show that response can be characterized at different thresholds, but they do not turn an imprecise primary comparison into a conclusive result. The registry lists further outcomes, including pharmacokinetic and antibody measures, but the evidence available in the posted summaries should not be interpreted as though every listed outcome had a reported and fully analyzed result.

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

• Overall Response Rate (ORR)
• Percentage of Participants Achieving Complete Response (CR) or Better
• Progression Free Survival (PFS)
• Overall Survival (OS)
• Percentage of Participants With Negative Minimal Residual Disease (MRD)
• Time to Next Treatment
• Serum Concentrations of Daratumumab
• Number of Participants With Anti-recombinant Human Hyaluronidase (rHuPH20) Antibodies

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant either met the registry’s definition of very good partial response or better during the stated response window or did not. A response percentage summarizes the number meeting that definition relative to the analysis population. The posted primary percentages are 46.2% for carfilzomib and dexamethasone and 48.8% for daratumumab with carfilzomib and dexamethasone. The registry also supplies confidence intervals and an unadjusted comparison p-value.

What does a confidence interval describe?

General statistical explanation: a confidence interval expresses uncertainty around an estimate under the assumptions of the method used to construct it. It is not a range that contains a fixed percentage of individual participants, and it is not a guarantee that the true response rate lies inside the particular interval. If the study and analysis were repeated many times under the same conditions, intervals built by a procedure with a stated confidence level would have a long-run coverage interpretation. The registry reports 90% confidence intervals for the primary response rates. The specific interval-construction method is not reported in the registry record.

The primary arm intervals are 32.3% to 60.4% and 35.1% to 62.6%. Their width conveys that the estimates are not highly precise. Comparing the arm intervals by eye is not a substitute for a formal comparison: overlap or lack of overlap between separate intervals is not itself the test of a difference. The registry reports an unadjusted p-value for the comparison, but does not report the detailed test specification or whether any covariate adjustment was considered.

What does the comparison p-value mean?

General statistical explanation: a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. Here the unadjusted p-value is 0.814. The registry does not provide a full statistical analysis entry that would allow the precise null hypothesis, test procedure, or any model details to be checked. It is therefore appropriate to report the posted value as unadjusted and to interpret it together with the estimates and their uncertainty.

For a binary endpoint, an absolute difference in response proportions is one possible way to describe the contrast between groups. A risk difference is expressed in percentage-point terms when proportions are displayed as percentages. The comparison display uses a risk-difference measure and gives its own uncertainty interval. That interval, rather than either arm-specific interval alone, is the relevant display for assessing the range of plausible differences under the reported analysis. No adjusted comparison is listed. The sponsor’s analysis therefore remains the relevant posted result; the record does not show a discrepancy requiring a recalculated result to take precedence.

Why does the analysis population matter?

The registry defines a response-evaluable analysis set consisting of participants with a confirmed diagnosis and measurable disease at baseline or screening. This definition establishes who was eligible for inclusion in the primary response calculation, but it does not explain the status of every enrolled participant. The registry does not report how missing response assessments, withdrawals, or participants who began subsequent anti-myeloma therapy before a response assessment were handled. Those details can affect the denominator and, in some circumstances, the estimated response percentage.

The primary arm denominators are 39 and 41, while the registry lists 88 participants enrolled and gives a safety at-risk denominator of 43 in each arm. These are distinct populations as presented in the record. They should not be treated as interchangeable or combined. A reason for the differences is not reported in the registry record. The randomized assignment is a feature of the design, but the posted response analysis set is specifically described as response-evaluable; the registry does not state that the primary result follows an intention-to-treat approach.

What can and cannot be inferred from the posted analysis?

General statistical explanation: randomization aims to make treatment groups comparable on average at assignment, while a parallel design compares groups treated during the same study. Neither feature removes uncertainty from a small sample. An open-label design means masking is absent; this can matter if knowledge of assignment influences response assessment or other study procedures. The registry does not report the steps used to reduce that possibility, so the degree of any influence cannot be determined from this record.

The registry lists 10 outcome measures and 0 analysis entries. This means the record contains posted outcome summaries but no detailed analysis entries in the registry record. It does not establish which analyses were planned in advance, whether interim analyses occurred, or how the final analysis choices were made. Those design and analysis details are not reported in the registry record. A small p-value threshold or a statistical model should not be imputed where the record does not state one.

General statistical explanation: when binary outcomes are rare or sample sizes are limited, estimates can be sensitive to a small number of participants, and interval methods may behave differently depending on the chosen procedure. A binomial model treats each participant’s outcome as a binary observation under the model assumptions. Over-dispersion is a general concern when outcomes vary more than a simple binomial model allows; whether it was assessed or relevant to the posted analysis is not reported in the registry record. These concepts help explain why analysis details matter, but they do not establish which methods the study used.

11. Confidence Intervals and Precision

The primary response percentages are estimates from a limited response-evaluable population. The registry reports 39 participants in the carfilzomib and dexamethasone arm and 41 in the daratumumab combination arm. Their 90% confidence intervals are 32.3% to 60.4% and 35.1% to 62.6%, respectively. Each interval covers a broad range of possible response rates, so the point estimates should not be treated as exact underlying rates.

The comparison display is important because the question is about the difference between assigned groups, not whether either group’s response rate differs from a fixed benchmark. Its interval includes values on both sides of no difference. This means the posted comparison is compatible with more than one direction of effect, as well as with little or no difference, under the reported uncertainty. The unadjusted p-value of 0.814 is consistent with the absence of a clear statistical separation in these results. It does not show that the groups are equivalent: demonstrating equivalence would require an appropriate design, a prespecified equivalence margin, and a corresponding analysis, none of which is reported in the registry record.

A confidence interval describes statistical uncertainty under its construction method; it does not capture every source of uncertainty. For example, it does not by itself address the possibility that the response-evaluable population differs from the enrolled population, uncertainty about missing assessments, the effects of an open-label design, or choices made in an analysis plan. The method used to construct the intervals is not reported in the registry record.

The additional response outcomes also have uncertainty intervals, as shown in the tables. Their precision should be judged from those intervals and their analysis denominators, not from point estimates alone. In this small study, all posted results are best read as estimates with limited precision rather than as exact forecasts for future participants or settings.

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 table and curve are planning illustrations based on the observed effect, not a record of the trial’s original design calculation. Because the outcomes are binary percentages, the illustrated sample sizes are participants per arm, not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm in a hypothetical future study that, under those planning assumptions and for the chosen effect, would have an 80% chance of detecting that effect using the stated significance threshold. The 90% power column describes the analogous planning target with a higher chance of detection. These figures are not guarantees: actual power depends on the true effect, event rates, analysis choices, and whether the assumptions hold. Smaller effects are harder to distinguish from random variation and therefore require more participants in the planning illustration.

Rows that plan for 100%, 75%, or 50% of the observed effect show how the planning requirement changes when the assumed effect is reduced. They are scenario comparisons, not alternative analyses of the participants in this study. The primary observed comparison is small relative to its uncertainty, so planning based on it produces a demanding illustration; this does not establish that any particular future study is necessary or feasible. These figures are not observed power. Observed power would not resolve the uncertainty in the posted result, and the table should be read as a planning aid rather than a retrospective test of whether this study was adequately designed.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.462; treatment proportion p₁ = 0.488; average p̄ = 0.475.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7062 = 1.3841.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7060 = 0.5941.
4. n = (1.3841 + 0.5941)² / (0.0263)² = 5,672.4, rounded up to 5,673 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
p0 <- 0.461538461538462                          # control proportion
p1 <- 0.48780487804878                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3871829)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 5,673 (80% power), 7,594 (90% power)
 75% of observed effect: n per arm = 10,079 (80% power), 13,492 (90% power)
 50% of observed effect: n per arm = 22,660 (80% power), 30,334 (90% power)
power.prop.test: 5672.4 
Simulated power at n = 5,673 per arm: 0.800 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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

Multiplicity arises when a study evaluates several outcomes, time points, subgroups, or statistical comparisons. Each additional test creates another opportunity for a result to look unusual by chance. The registry lists multiple secondary outcomes alongside the primary endpoint. It does not report a multiplicity strategy, a hierarchy of tests, or whether the secondary analyses were intended to be confirmatory. The posted secondary results therefore warrant more caution than a single prespecified primary test.

The primary comparison is reported with an unadjusted p-value. The registry also lists 0 analysis entries. No multiplicity-adjusted p-values or other adjustment procedures are reported in the registry record. This does not show that no such planning occurred outside the registry; it means the record does not document it. Without a stated plan, the reader cannot determine how the reported secondary comparisons relate to any overall error-control strategy.

Missing data and analysis populations are also important. The primary outcome is described for a response-evaluable set requiring confirmed multiple myeloma and measurable disease at baseline or screening. The posted primary denominators are 39 and 41, while the registry lists 88 enrolled and 43 participants at risk in each arm for the safety summaries. The record does not explain why these denominators differ, how missing response assessments were handled, or whether participants without an evaluable assessment were counted as nonresponders. It also does not report a sensitivity analysis for missing outcomes.

The outcome definition ends the response window before subsequent anti-myeloma therapy begins. The registry does not describe how participants who started subsequent therapy before an assessment, or who discontinued study treatment, were handled in the analysis. These details could affect the observed response classification and the population contributing to the result. The registry does not report an intention-to-treat analysis for the primary endpoint, nor does it state the analysis population used for every secondary outcome.

Interim analyses, stopping rules, sample-size justification, and the original statistical analysis plan are not reported in the registry record. The terminated status does not by itself explain whether or how these factors affected the posted results. Readers should distinguish what the record states from what is unknown: the trial was randomized, the primary endpoint and response-evaluable population are described, and the estimates are posted, while important analysis and missing-data details remain undocumented.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (9.3%), acute kidney injury (9.3%), covid-19 (7.0%), cardiac failure (4.7%), pyrexia (4.7%).

The safety display reports 43 participants at risk in each arm. In the carfilzomib and dexamethasone group, 20 participants are listed with serious adverse events and 39 with other adverse events; 12 deaths are recorded. In the group receiving daratumumab with those drugs, 12 participants are listed with serious adverse events and 37 with other adverse events; 8 deaths are recorded. These are counts in the registry’s safety display, not estimates of a causal treatment effect.

The registry lists pneumonia and acute kidney injury at 9.3% each among the leading serious adverse-event terms, followed by COVID-19 at 7.0%, and cardiac failure, pyrexia, and dyspnoea at 4.7% each. The available listing does not assign these terms to a specific arm, so they should not be interpreted as arm-specific rates. The record does not state that the deaths were caused by study treatment, and these counts should not be described as treatment-related deaths.

Serious adverse events and other adverse events are different categories in the display. The figures should be read with their denominators and the registry’s definitions, which are not detailed. They do not establish comparative safety on their own, particularly without information on event timing, exposure duration, relatedness, or statistical comparisons. Such details are not reported in the registry record.

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

The result does show what happened in the posted response-evaluable analysis: the registry reports a very good partial response or better rate of 46.2% with carfilzomib and dexamethasone and 48.8% with daratumumab added to those drugs. The corresponding 90% confidence intervals are broad, and the posted unadjusted p-value is 0.814. The observed rates are close, but the study does not estimate the group difference precisely enough to rule out a range of possible differences.

That result does not establish equivalence, non-inferiority, or absence of an effect. Those conclusions require an appropriate design and analysis, including prespecified criteria; such criteria are not reported in the registry record. Nor does the result establish that either regimen is effective or ineffective. This page describes statistical results and uncertainty, not a treatment recommendation.

The endpoint measures response under specified disease criteria, not survival, duration of response, quality of life, or every other outcome that may matter. The registry lists progression-free survival, overall survival, time to next treatment, and other outcomes, but their results are not available in the quantitative summaries. A response percentage should not be used as a substitute for those measures.

The study was randomized and parallel-group, which supports a between-group comparison, but it was open-label and had a small response-evaluable population. The record does not report enough detail to assess all possible effects of missing assessments, analysis choices, or early termination. The reason for termination is not reported in the registry record. Those limitations constrain how broadly the findings can be interpreted.

The most balanced conclusion is that the posted primary results are descriptive and imprecise. They do not show a clear statistical separation between the groups in this trial, but they also do not demonstrate that the treatment strategies have the same effect. The confidence intervals, denominators, and missing analysis details are central to that interpretation.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an observed estimate and a precise estimate. The two primary response percentages are close, but their confidence intervals cover broad ranges. A small distance between point estimates should not be mistaken for evidence that the underlying effects are identical, and a nonsignificant comparison should not be treated as proof of no effect. The result needs to be read as an uncertain comparison, not a definitive verdict.

The record also highlights the importance of specifying the analysis population. The primary response endpoint uses a response-evaluable set, the safety display uses a different at-risk count, and the enrollment figure is separate from both. Those numbers serve different purposes. Understanding which participants contribute to each result is essential before interpreting percentages or comparing endpoints.

Another statistical lesson is that a primary endpoint and secondary outcomes answer different questions. A response threshold can be clinically meaningful as a measure of disease response, while survival and other outcomes capture different dimensions. A collection of secondary outcomes can add context, but without a documented multiplicity strategy and analysis plan, secondary comparisons should not be used to override an uncertain primary result.

Finally, a planning illustration based on the observed effect is not a retrospective measure of study quality. It shows how the required sample size changes under stated hypothetical assumptions and effect sizes. It cannot tell readers whether the original design was adequate, because the original design assumptions are not reported in the registry record. The distinction between a planning calculation and observed power is particularly important when interpreting a small study with wide intervals.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations are specific to the information available for this trial. The registry lists the study as terminated but does not report the reason for termination. It is therefore not possible from this record to assess whether termination was related to recruitment, an operational issue, safety, efficacy, or another cause. The record does not describe whether termination altered the intended timing or scope of the final analysis.

The primary result is based on 39 and 41 response-evaluable participants, while 88 participants are listed as enrolled. The safety display lists 43 at risk in each group. The record does not reconcile these populations or explain the handling of participants without an evaluable primary response. This limits assessment of potential selection and missing-data effects. The primary endpoint’s response-evaluable definition is available, but details of exclusions and sensitivity analyses are not reported in the registry record.

The study was open-label, and the registry does not report whether response assessments were independently reviewed or otherwise protected from knowledge of assigned treatment. That does not show that assessments were biased; it leaves a relevant design detail unknown. The record also does not provide detailed randomization procedures, allocation ratio, or stratification factors.

The posted primary intervals are wide, and the sample is limited. Statistical analysis entries are not posted, while the original sample-size justification, interim analyses, multiplicity plan, missing-data methods, and detailed statistical analysis plan are not reported in the registry record. The secondary outcomes include several measures, but not all have quantitative summaries in the results. These gaps mean the registry results support a cautious descriptive interpretation, not a complete reconstruction of the trial’s design or analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Daratumumab Retreatment in Participants With Multiple Myeloma Who Have Been Previously Treated With Daratumumab — NCT03871829.
• Registry record last updated 2025-03-30; status last verified 2025-03.
• Results first posted 2023-12-19.
• 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

This terminated phase 2 randomized, parallel-group study compared carfilzomib and dexamethasone with daratumumab subcutaneous added to carfilzomib and dexamethasone in participants with multiple myeloma previously treated with daratumumab. The study enrolled 88 participants and was not masked.

The primary endpoint was the percentage achieving very good partial response or better. The registry reports rates of 46.2% and 48.8% in the two groups, with 90% confidence intervals of 32.3% to 60.4% and 35.1% to 62.6%, and an unadjusted comparison p-value of 0.814. The estimates are imprecise, and the record does not establish equivalence or a definitive treatment-group difference.

The primary analysis population, safety denominators, and enrollment count are not identical. Reasons for those differences, the reason for termination, and important statistical-plan and missing-data details are not reported in the registry record. Secondary findings and safety counts should be read as descriptive, with the limitations of the posted analyses in mind.