Phase 3 Study With Carfilzomib and Dexamethasone Versus Bortezomib and Dexamethasone for Relapsed Multiple Myeloma Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Study With Carfilzomib and Dexamethasone Versus Bortezomib and Dexamethasone for Relapsed Multiple Myeloma Patients (NCT01568866), a randomized phase 3 study. The primary outcome is Progression-free Survival.

2. Clinical Question

3. Trial Design

This was a randomized, open-label, parallel-group phase 3 study. Participants were assigned to carfilzomib plus dexamethasone or bortezomib plus dexamethasone. The registry record reports 929 enrolled participants: 464 in the carfilzomib group and 465 in the bortezomib group for the primary outcome. The study is marked completed.

The population of interest had multiple myeloma relapsed after 1 to 3 prior therapies. The primary outcome was progression-free survival, assessed in the intent-to-treat population. The record describes disease response and progression assessment according to the International Myeloma Working Group-Uniform Response Criteria, as assessed by an Independent Review Committee.

The regimens had different administration schedules and cycle lengths. Carfilzomib was administered intravenously, with an initial dose schedule followed by 56 mg/m² dosing on specified days in 28-day cycles. Bortezomib was administered intravenously or subcutaneously on specified days of a 21-day cycle. Dexamethasone accompanied both regimens. The full carfilzomib-arm dexamethasone schedule is not reported in the registry record.

Because masking was absent, treatment assignment was known to participants and study personnel. The registry record does not report the original sample-size justification, allocation concealment procedures, or details of any interim monitoring. Those omissions limit what can be concluded about aspects of the planned conduct beyond the randomized, open-label, parallel-group design.

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: Randomization was stratified by previous proteasome inhibitor therapy (yes vs no), previous lines of treatment (1 vs 2 or 3), International Staging System stage (I vs II-III), and planned route of bortezomib administration (intravenous vs subcutaneous) if randomly assigned to the bortezomib group.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat population

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: Intent-to-treat population (all randomized participants)

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival, measured over From randomization until the data cut-off date of 10 November 2014; median follow-up time for PFS was 11.1.and 11.9 months in the bortezomib and carfilzomib arms respectively.

Progression-free survival was the primary endpoint. It measures the time from randomization until the earlier of documented disease progression or death from any cause. It is used in trials of relapsed multiple myeloma because it captures both worsening disease and death within one time-to-event outcome, rather than counting only one kind of event.

The registry record states that disease response and progression were assessed using International Myeloma Working Group-Uniform Response Criteria, with assessments made by an Independent Review Committee. Median progression-free survival was estimated with the Kaplan-Meier method. A median is the estimated time by which half of the analyzed population has experienced the event, subject to the assumptions of the time-to-event analysis.

Participants without a documented event by the data cut-off could be censored. The record also describes censoring in several other circumstances, including starting new anticancer therapy before a progression or death was documented, and missing disease assessments followed by an event or no documented event before cut-off. Censoring allows participants with incomplete event-time information to contribute until the point at which their status is no longer observed. It relies on assumptions about the relationship between censoring and the chance of the event; the registry record does not report analyses testing those assumptions.

7. Results Posted in the Registry

• Bortezomib + DEX vs Carfilzomib + DEX: hazard ratio 0.53 (95% CI 0.44–0.65), reported p < 0.001 (as reported in the registry).

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 Survival

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Stratified Log Rank); it was not recalculated.
• Result:
  • Bortezomib + DEX vs Carfilzomib + DEX: hazard ratio 0.79 (95% CI 0.65–0.96), reported p = 0.010 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Bortezomib + DEX vs Carfilzomib + DEX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Response

• 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:
  • Carfilzomib + DEX: 76.9% (357/464) versus 62.6% (291/465) on control; risk difference 14.4 percentage points (95% CI 8.5 to 20.2), risk ratio 1.23 (1.13–1.34); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Carfilzomib + DEX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With ≥ Grade 2 Peripheral Neuropathy

• 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:
  • Carfilzomib + DEX: 6.0% (28/463) versus 32.0% (146/456) on control; risk difference -26.0 percentage points (95% CI -30.8 to -21.2), risk ratio 0.19 (0.13–0.28); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Carfilzomib + DEX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the assessment beyond time without progression or death. Overall survival provides a later time-to-event outcome, overall response describes tumor response during treatment, and peripheral neuropathy captures a selected adverse outcome. Other posted outcomes concern response duration and measures of cardiac or pulmonary status. These endpoints address distinct aspects of disease course and safety, so they complement rather than duplicate the primary endpoint.

Across the posted results, the reported patterns are not all expressed on the same scale: time-to-event outcomes use medians and hazard ratios, response uses a proportion and odds ratio, and peripheral neuropathy uses a proportion and odds ratio. The direction of each arm-level result can be considered within its own outcome, but comparisons across unlike outcomes do not establish a single overall benefit-harm measure. The clinical significance of secondary differences cannot be determined from statistical summaries alone.

Secondary findings generally carry less inferential weight when many outcomes are tested without an adjustment for multiplicity. Repeated testing increases the opportunity for a nominally unusual result to occur by chance across the family of analyses. The registry record does not report a multiplicity procedure or a hierarchy for secondary endpoints. This does not erase the observed estimates, but it means that isolated secondary p-values should be interpreted cautiously and alongside effect estimates, confidence intervals, endpoint definitions, and follow-up.

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

• Overall Survival
• Overall Response
• Duration of Response
• Percentage of Participants With ≥ Grade 2 Peripheral Neuropathy
• Percentage of Participants With a Significant Reduction in Left Ventricular Ejection Fraction (LVEF)
• Change From Baseline in Right Ventricular Fractional Area Change (FAC)
• Change From Baseline in Pulmonary Artery Systolic Pressure (PASP)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. Participants enter the risk set at randomization and are followed until progression or death, or until a censoring event. The Kaplan-Meier method estimates the probability of remaining free of the event over time while accounting for differing follow-up lengths and censored observations. In general, this method assumes that censoring does not carry unaccounted information about the event risk after the censoring time. Whether that assumption was examined is not reported in the registry record.

What does the median represent?

The median progression-free survival is the estimated time at which the Kaplan-Meier event-free probability reaches one half. It is a summary of the estimated survival curve, not an average event time and not a guarantee about an individual participant’s course. The confidence interval communicates uncertainty in the estimated median. When one confidence limit is not reported, the record does not provide a complete interval from which to describe uncertainty on that side.

How should a hazard ratio be read?

A hazard ratio compares event rates over follow-up under a model or analysis contrast; it is not the same as a ratio of median times. In general, a hazard ratio less than 1 indicates a lower instantaneous event hazard for the numerator group relative to the denominator group, if the contrast is defined in that direction and the model’s interpretation is appropriate. The registry reports a hazard ratio for the primary outcome but does not clearly state its treatment-group orientation in the displayed comparison description. The sponsor’s own contrast definition is therefore needed to assign direction. The reported confidence interval gives a range of values compatible with the analysis under its assumptions.

The primary comparison used a stratified log-rank method. In general, the log-rank test compares time-to-event experience between groups over follow-up, and stratification can account for prespecified strata in the comparison. The strata and their role are not reported in the registry record. The reported p-value is evidence against the null hypothesis used by that test, not a measure of effect size, clinical importance, or the probability that the null hypothesis is true.

How do the binary outcomes differ?

Overall response and peripheral neuropathy are reported as percentages of participants meeting a binary outcome definition. For these outcomes, the registry also reports sponsor analyses using a stratified Cochran-Mantel-Haenszel method and odds ratios. In general, an odds ratio compares the odds of an outcome between groups; it is not a risk difference and does not directly state the change in outcome probability. The stratified form accounts for grouping factors in the analysis, though those factors are not specified in the record.

The posted re-calculations for binary outcomes are simple, unadjusted comparisons derived from the arm-level summaries. They include a risk difference and its confidence interval, which express the absolute difference between the observed group proportions. These unadjusted results do not incorporate the sponsor analysis’s stratification. Differences between such estimates and adjusted analyses can arise because they answer the comparison using different methods, not necessarily because either calculation is erroneous. The registry’s reported sponsor analysis remains the appropriate reference for its stated analysis.

Why does over-dispersion matter in general?

Over-dispersion occurs when observed variability is greater than assumed by a model. If it is ignored, standard errors can be too small and confidence intervals too narrow, making the analysis appear more precise than warranted. The registry record does not report an over-dispersion assessment or identify a model requiring that adjustment for the posted primary outcome.

For all methods, estimates depend on the population analyzed, outcome definitions, follow-up, censoring, and model assumptions. The intent-to-treat population is named for the primary outcome, but the registry record does not provide a full statistical analysis plan or detailed missing-data procedures. These omissions constrain independent assessment of some analytic choices.

11. Confidence Intervals and Precision

The primary median estimates are accompanied by 95% confidence intervals. For bortezomib plus dexamethasone, the median progression-free survival is 9.4 months, with an interval from 8.4 to 10.4 months. For carfilzomib plus dexamethasone, the median is 18.7 months, with a lower confidence limit of 15.6 months; an upper limit is not reported in the registry record. A confidence interval describes uncertainty in an estimate under the method’s assumptions. It is not a range containing the true value with a 95% probability after the data have been observed.

The reported primary hazard ratio is 0.533, with a 95% confidence interval from 0.437 to 0.651. The interval communicates uncertainty in the relative time-to-event comparison, but its treatment direction depends on the contrast orientation, which is not clear in the registry comparison label. The registry also reports a very small p-value for this analysis; statistical evidence and precision are related but not interchangeable. A p-value does not describe the range of plausible effect sizes.

For the secondary outcomes, the registry reports confidence intervals for arm-level estimates and sponsor comparisons. The width of an interval reflects both the amount of information and variability under the analysis. More follow-up or more observed events can improve information for time-to-event outcomes, while participant counts and event frequency contribute to precision for binary outcomes. Precision should not be confused with clinical importance. The record’s incomplete upper confidence limit for the primary median in the carfilzomib group is an important reporting limitation when assessing the estimate’s full uncertainty.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations use the observed effect as a starting point and show how required sample size changes when the effect to detect is set to different fractions of that observed effect. For the time-to-event outcomes, the figures are total events, not participants per arm. For the other outcomes, they are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Time-to-event illustrations use the Schoenfeld approach.

The 80% power column describes the number of events or participants required, under those assumptions, for an 80% chance of detecting the stated effect if that effect is real. The 90% power column gives the corresponding requirement for a 90% chance. These are planning probabilities for hypothetical repeated studies, not guarantees about a particular trial’s result. Smaller effects are harder to distinguish from random variation, so the illustrations require more events or participants when the target is a smaller fraction of the observed effect.

These figures are planning illustrations based on the observed effect, not observed power. The trial’s original design assumptions and sample-size justification are not reported in the registry record. The illustrations should therefore not be interpreted as evidence that the study was originally designed around these assumptions, nor as a reconstruction of the sponsor’s actual planning process.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.533, so ln(HR) = -0.6292.
2. d = 4 × (1.96 + 0.842)² / [ln(0.533)]² = 79.3, rounded up to 80 events in total 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
hr <- 0.533                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(1568866)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 80 (80% power), 107 (90% power)
 75% of observed effect: events = 141 (80% power), 189 (90% power)
 50% of observed effect: events = 318 (80% power), 425 (90% power)
Simulated power with 80 events: 0.805 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 135 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 929 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 9.4          # control-arm median, months (converted from the posted unit)
hr          <- 0.533          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 102         p (1-sided)   0.0001
  Events: 36        ~HR at bound   0.2871
   Month: 18    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.53   0.0338
   IA 2: 67%                   Z   2.5114
      N: 136         p (1-sided)   0.0060
  Events: 71        ~HR at bound   0.5503
   Month: 29    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.53   0.5603
       Final                   Z   1.9930
      N: 136         p (1-sided)   0.0231
 Events: 107        ~HR at bound   0.6791
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.53   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The registry’s primary time-to-event analysis reports a stratified log-rank hazard ratio and its confidence interval. No independent recalculated hazard ratio is used for the primary outcome; the displayed time-to-event comparison relies on the sponsor-reported estimate. The orientation of the reported contrast is not clear from the registry’s comparison label, so its direction should be checked against the sponsor’s analysis definition before associating a hazard ratio less than 1 with a specific arm.

For binary secondary outcomes, the sponsor reports stratified Cochran-Mantel-Haenszel odds ratios. The accompanying unadjusted re-calculations use arm-level counts to estimate simple group differences and are not substitutes for the sponsor’s stratified analysis. Such re-calculations are useful for understanding the raw absolute contrast but do not reproduce adjustments or stratification used in the sponsor analysis.

The registry does not flag a discrepancy between the posted summary information and sponsor analysis. Nevertheless, method and estimand matter: an unadjusted risk difference and a stratified odds ratio are different summaries, and their numerical values should not be treated as interchangeable. The sponsor’s reported analysis is the reference for the inferential result stated in the registry.

16. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is identified as progression-free survival, but the registry record does not report a complete statistical analysis plan specifying how the primary and secondary hypotheses were organized. It also does not report whether interim analyses were conducted, whether any alpha-spending procedure was used, or how multiplicity across secondary endpoints was handled. Those details matter because repeated testing can raise the chance of at least one apparently positive result when all null hypotheses are true.

Seven secondary outcomes are listed, including overall survival, overall response, duration of response, peripheral neuropathy, and measures of cardiac and pulmonary function. The presence of several outcomes is not itself evidence of a problem; it does mean that inferential claims should distinguish the designated primary result from additional analyses. Without a reported testing hierarchy or multiplicity adjustment, secondary p-values are best treated as exploratory evidence rather than as a set of equally confirmatory conclusions.

The primary outcome is described for the intent-to-treat population. The registry explains censoring rules for progression-free survival, including censoring participants who began new anticancer therapy before documented progression or death, and some participants with missing assessment visits. It does not report whether sensitivity analyses tested alternative censoring assumptions, how missing covariates were handled, or whether any imputation was used for missing data in other outcomes.

The reported analysis population and censoring rules help clarify how observations entered the primary analysis, but they do not resolve all potential missing-data concerns. In general, censoring can bias a time-to-event estimate if the likelihood of becoming censored is related to the event risk in ways not accounted for by the analysis. The registry record does not describe such diagnostic checks. The original sample-size justification and interim-monitoring plan are also not reported in the registry record.

17. Safety Results

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

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 (9.2%), pyrexia (4.1%), dyspnoea (3.9%), diarrhoea (2.4%), renal failure acute (2.4%).

The adverse-event summaries report serious adverse events among 182 of 456 participants at risk in the bortezomib group and 272 of 463 participants at risk in the carfilzomib group. Other adverse events are reported among 435 of 456 and 446 of 463 participants, respectively. These are counts of participants with events, not counts of individual event episodes. The record does not report deaths in these summaries.

The most frequently listed serious adverse-event terms include pneumonia, pyrexia, dyspnoea, diarrhoea, acute renal failure, and respiratory tract infection. The registry gives percentages for these terms, but the summary does not establish from the listed information whether each percentage is arm-specific or pooled. They should therefore not be assigned to a particular treatment group without further detail.

These safety figures are descriptive. They do not by themselves establish a causal difference between regimens, and the record does not provide a full account of event severity, duration, treatment attribution, or exposure-adjusted rates. Median treatment duration differed between groups for some reported outcomes, which can affect the opportunity to observe adverse events. The posted counts should be interpreted with these limitations in mind.

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

The primary outcome estimates describe progression-free survival in a randomized, open-label trial of two active regimens among participants with relapsed multiple myeloma after 1 to 3 prior therapies. The registry reports longer median progression-free survival for the carfilzomib group than for the bortezomib group, with confidence intervals describing uncertainty in those estimates. The sponsor’s stratified log-rank analysis also reports a hazard ratio and a small p-value, although the treatment-group orientation of that ratio is not clear from the registry’s comparison label.

These findings do not establish that every participant benefited to the same extent, or that a median predicts an individual participant’s outcome. They do not show what would happen in people outside the stated population, under different treatment schedules, or with different prior treatment histories. The trial’s open-label conduct also means treatment assignment was known, although the primary progression and response assessments were made by an Independent Review Committee.

The results do not, by themselves, settle the overall balance of efficacy and harms. The posted secondary and safety outcomes add information, but they are distinct measures and multiplicity handling is not reported. The registry record also does not contain the complete statistical analysis plan or all details needed to examine missing-data assumptions. Statistical significance should not be confused with clinical importance, and a confidence interval does not resolve the relevance of an effect for every patient or setting.

19. Why This Trial Matters Statistically

Statistically, the study illustrates how a randomized comparison can be described using more than one summary of a time-to-event outcome. The arm-level medians provide an interpretable time scale, while the log-rank analysis and hazard ratio summarize a relative comparison over follow-up. These quantities answer related but different questions; the hazard ratio is not a ratio of medians, and its direction depends on how the contrast is defined.

The record also illustrates the role of independent review and explicit censoring rules in progression-free survival analyses. Such details affect which observations contribute information and how the event-time distribution is estimated. At the same time, the incomplete upper confidence limit for one primary median and the unclear hazard-ratio orientation in the comparison label demonstrate why careful attention to reporting format is essential.

Finally, the trial provides secondary response, survival, and safety summaries alongside the primary endpoint. These can enrich interpretation, but a collection of outcomes calls for attention to multiplicity, differing outcome scales, and the distinction between adjusted sponsor analyses and unadjusted arm-level comparisons. The registry record makes some of these results available while leaving key planning and analysis details unreported, underscoring the importance of transparent protocols and statistical plans for evaluating trial evidence.

20. 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 leaves several trial-specific uncertainties. The hazard-ratio comparison is labeled with the bortezomib and carfilzomib arms in an order that does not make the reported ratio’s numerator and denominator clear. That ambiguity limits interpretation of the ratio’s direction without the sponsor’s contrast definition. In addition, the upper confidence limit for median progression-free survival in the carfilzomib group is not reported, leaving its interval incomplete.

Median follow-up for progression-free survival was 11.1 months in the bortezomib group and 11.9 months in the carfilzomib group. The primary outcome cut-off was 10 November 2014. These follow-up details are relevant because later event times are less fully observed when follow-up is shorter, and the median follow-up values are not measures of the maximum follow-up for every participant.

The study was open-label. Although an Independent Review Committee assessed response and progression, the registry does not report details of allocation concealment, stratification factors, or procedures to maintain assessment independence. The record also does not report the original sample-size justification, interim analyses, multiplicity control, or the complete statistical analysis plan.

Safety reporting is limited to selected summary counts and listed serious adverse-event terms. The available record does not report deaths in the safety summaries or enough detail to assess exposure-adjusted event rates and treatment attribution. The carfilzomib-arm dexamethasone schedule is incomplete in the registry description. These limitations constrain a full appraisal of design, safety, and analysis choices from the registry record alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Phase 3 Study With Carfilzomib and Dexamethasone Versus Bortezomib and Dexamethasone for Relapsed Multiple Myeloma Patients — NCT01568866.
• Registry record last updated 2022-11-14; status last verified 2022-11.
• Results first posted 2015-12-11.
• 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.

24. Record Summary

NCT01568866 is a completed randomized, open-label, parallel-group phase 3 study in multiple myeloma. It compared carfilzomib plus dexamethasone with bortezomib plus dexamethasone in participants whose disease had relapsed after 1 to 3 prior therapies. The primary endpoint was progression-free survival in the intent-to-treat population, assessed through the data cut-off of 10 November 2014.

The registry reports arm-level median progression-free survival estimates, confidence intervals, and a stratified log-rank hazard ratio. Secondary outcomes include overall survival, response, and selected adverse outcomes. The record also provides serious and other adverse-event counts. The original sample-size rationale, full analysis plan, interim-analysis details, and multiplicity procedures are not reported in the registry record.