Study to Determine Efficacy and Safety of Lenalidomide Plus Low-dose Dexamethasone Versus Melphalan, Prednisone, Thalidomide in Patients With Previously Untreated Multiple Myeloma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Determine Efficacy and Safety of Lenalidomide Plus Low-dose Dexamethasone Versus Melphalan, Prednisone, Thalidomide in Patients With Previously Untreated Multiple Myeloma (NCT00689936), a randomized phase 3 study. The primary outcome is Kaplan-Meier Estimates of Progression-free Survival (PFS) Based on the Response Assessment by the Independent Review Adjudication Committee (IRAC).

2. Clinical Question

3. Trial Design

This was a randomized, open-label, parallel-group phase III trial with three treatment arms. The registry reports enrollment of 1623 participants and identifies previously untreated multiple myeloma as the condition studied. Eligible participants were described as 65 years of age or older or not candidates for stem cell transplantation. The study is marked completed in the registry record.

Participants were assigned to lenalidomide plus low-dose dexamethasone until disease progression, the same drug combination for 18 four-week cycles, or melphalan, prednisone, and thalidomide for 12 six-week cycles. Because masking was absent, participants and study teams knew the assigned treatment. The primary progression-free survival assessment was based on review by the Independent Review Adjudication Committee (IRAC), which is distinct from the investigator-assessed response outcomes also recorded.

The primary outcome was a time-to-event measure: progression-free survival from randomization to documented disease progression or death, whichever occurred first. Its stated assessment period ran from randomization to the data cut-off date of 24 May 2013, with median follow-up of 17.1 months. The registry also lists a final overall survival analysis with median follow-up of 48.3 months. It does not report the original sample-size justification, the planned allocation ratio, or a detailed statistical analysis plan.

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: Participants were stratified at randomization by 1) age (≤ 75 versus \> 75 years), 2) stage (International Staging System Stages I or II versus Stage III), and 3) country.

Active Treatment Phase

Reasons for not completing this period:

Progression Free Survival-PFS-Follow-Up

Long-Term Follow Up Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intent to treat (ITT) population included all participants who were randomized, independent of whether they received study treatment or not.

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 (ITT) population includes all participants who were randomized, independent of whether they received study treatment or not

6. Primary Endpoint

The registry lists the primary outcome as Kaplan-Meier Estimates of Progression-free Survival (PFS) Based on the Response Assessment by the Independent Review Adjudication Committee (IRAC), measured over From date of randomization until the data cut-off date of 24 May 2013. Median follow-up time for all participants was 17.1 months..

The primary endpoint was progression-free survival (PFS), measured from randomization until the first documented disease progression or death from any cause, whichever came first. Disease progression was assessed using International Myeloma Working Group Uniform Response criteria, and the primary PFS assessment was based on IRAC review. PFS is used in trials as a time-to-event measure that captures how long participants remain alive without documented progression. It therefore combines progression and death into one endpoint rather than treating response at a single assessment as the whole clinical course.

The registry reports Kaplan-Meier estimates of median PFS for each randomized group, alongside hazard ratios for pairwise comparisons. Kaplan-Meier methods account for participants whose event status is not observed for the full follow-up period by incorporating censoring. The registry describes censoring for reasons including withdrawal, starting another anti-myeloma therapy without documented progression, and certain missing or delayed assessments. The particular endpoint definition and censoring rules matter: the estimated PFS depends on when progression or death is recorded and on how incomplete follow-up is handled.

The ITT population was defined as all randomized participants, regardless of whether they received study treatment. This preserves the randomized group comparison as the basis for the primary analysis.

7. Results Posted in the Registry

• Lenalidomide and Low-Dose Dexamethasone (Rd) vs Melphalan + Prednisone + Thalidomide (MPT): hazard ratio 0.72 (95% CI 0.61–0.85), reported p < 0.001 (as reported in the registry).
• Lenalidomide and Low-Dose Dexamethasone (Rd) vs Lenalidomide and Dexamethasone Rd18: hazard ratio 0.70 (95% CI 0.60–0.82), reported p < 0.001 (as reported in the registry).
• Lenalidomide and Dexamethasone Rd18 vs Melphalan + Prednisone + Thalidomide (MPT): hazard ratio 1.03 (95% CI 0.89–1.20), reported p = 0.703 (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.

Kaplan Meier Estimates of Overall Survival at the Time of Final Analysis (OS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Lenalidomide and Low-Dose Dexamethasone (Rd) vs Melphalan + Prednisone + Thalidomide (MPT): hazard ratio 0.78 (95% CI 0.67–0.92), reported p = 0.002 (as reported in the registry).
  • Lenalidomide and Low-Dose Dexamethasone (Rd) vs Lenalidomide and Dexamethasone Rd18: hazard ratio 1.02 (95% CI 0.86–1.20), reported p = 0.829 (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 Lenalidomide and Low-Dose Dexamethasone (Rd) vs Melphalan + Prednisone + Thalidomide (MPT) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Lenalidomide and Low-Dose Dexamethasone (Rd) vs Lenalidomide and Dexamethasone Rd18 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With an Objective Response Based on IRAC Review

• 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:
  • Lenalidomide and Dexamethasone Rd18: 73.4% (397/541) versus 75.1% (402/535) on control; risk difference -1.8 percentage points (95% CI -7.0 to 3.5), risk ratio 0.98 (0.91–1.05); unadjusted two-proportion z-test p = 0.510.
  • Melphalan + Prednisone + Thalidomide (MPT): 62.3% (341/547) versus 75.1% (402/535) on control; risk difference -12.8 percentage points (95% CI -18.3 to -7.3), risk ratio 0.83 (0.76–0.90); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lenalidomide and Dexamethasone Rd18 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Melphalan + Prednisone + Thalidomide (MPT) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With an Objective Response Based on Investigator Assessment at Time of Final Analysis

• 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:
  • Lenalidomide and Dexamethasone Rd18: 78.6% (425/541) versus 80.7% (432/535) on control; risk difference -2.2 percentage points (95% CI -7.0 to 2.6), risk ratio 0.97 (0.92–1.03); unadjusted two-proportion z-test p = 0.372.
  • Melphalan + Prednisone + Thalidomide (MPT): 67.5% (369/547) versus 80.7% (432/535) on control; risk difference -13.3 percentage points (95% CI -18.4 to -8.1), risk ratio 0.84 (0.78–0.90); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lenalidomide and Dexamethasone Rd18 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Melphalan + Prednisone + Thalidomide (MPT) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several related but distinct aspects of disease course: overall survival, objective response, duration of response, time to first response, and time to treatment failure. The overall direction of the posted results is broadly consistent with the primary PFS comparison of the until-progression regimen against MPT. Comparisons between the two lenalidomide schedules do not show the same clear separation in the reported time-to-event summaries. Response summaries also follow a broad pattern in which the lenalidomide groups are closer to each other than either is to MPT.

These outcomes add context rather than replace the primary endpoint. Overall survival concerns death, whereas PFS includes progression or death. Response records whether a response was achieved under the outcome definition, while duration and timing measures address what followed or when a response first occurred. Their results can therefore differ without being logically inconsistent. The registry lists a wider set of secondary outcomes than the numeric summaries described in the posted results, so not every listed outcome can be interpreted from the available estimates.

Secondary comparisons carry less weight when many outcomes and comparisons are assessed without a reported multiplicity adjustment. With many tests, the chance of at least one apparently notable result arising by chance can increase. The registry does not report an adjustment strategy for the secondary analyses. Accordingly, these findings are best treated as supportive or exploratory context, not as a collection of independent confirmatory conclusions. The primary PFS result remains the designated main endpoint, while secondary patterns should be considered alongside the number of analyses and the uncertainty around each estimate.

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

• Kaplan Meier Estimates of Overall Survival at the Time of Final Analysis (OS)
• Percentage of Participants With an Objective Response Based on IRAC Review
• Percentage of Participants With an Objective Response Based on Investigator Assessment at Time of Final Analysis
• Kaplan Meier Estimates of Duration of Myeloma Response as Determined by the IRAC
• Kaplan Meier Estimates of Duration of Myeloma Response as Determined by an Investigator Assessment at Time of Final Analysis
• Time to First Response Based on the Review by the IRAC
• Time to First Response Based on the Investigator Assessment at the Time of Final Analysis
• Kaplan Meier Estimates of Time to Treatment Failure (TTF)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time to an event, rather than a simple count of whether an event ever occurred. The reported median is the time at which the Kaplan-Meier estimated event-free proportion reaches its midpoint. It describes the middle of the estimated PFS distribution; it is not an average duration for every participant and does not imply that all participants experienced an event at that time. Follow-up and censoring affect the estimate, so the stated follow-up period and censoring rules are important context.

What does a hazard ratio describe?

A hazard ratio compares the estimated event rates over time between two groups, accounting for the timing of events and censoring. A value of 1 corresponds to equal estimated hazards; a value below 1 indicates a lower estimated hazard in the first named group relative to the second, while a value above 1 indicates a higher estimated hazard. It is a relative time-to-event measure, not a difference in median months, and it does not by itself state how many participants had an event. The registry labels these as reported hazard ratios and gives log-rank tests for the comparisons.

The proportional-hazards interpretation is most straightforward when the relative hazards remain reasonably stable over follow-up. Whether that assumption was assessed, and whether the sponsor used other modeling checks, is not reported in the registry record. The available summary does not permit reconstruction of individual participant event times or independent verification of those modeling choices.

Why use Kaplan-Meier estimates?

Kaplan-Meier estimation accommodates incomplete observation by using the information available up to each participant’s last observed time. A participant who has not had a documented event when follow-up ends can contribute information until censoring, rather than being treated as if an event occurred or as if follow-up continued indefinitely. This relies on assumptions about censoring and the observation process. The registry lists several circumstances in which PFS observations were censored, including withdrawal, new anti-myeloma treatment before documented progression, and specified assessment gaps. It does not report additional sensitivity analyses for those rules.

The log-rank test compares event-time patterns between groups. The p-values reported for the PFS contrasts are tests of the corresponding group comparisons; they are not the probability that a treatment effect is true, nor do they indicate the size or clinical importance of an effect. The effect estimate and its confidence interval are needed to understand magnitude and uncertainty alongside the test result.

How should the response analyses be distinguished?

Objective response is a binary outcome: whether a participant met the response definition during the assessment period. The registry gives response percentages and sponsor-reported Fisher exact comparisons expressed as odds ratios. An odds ratio compares the odds of response, not response percentages directly. The displayed percentage summaries and the odds-ratio comparisons therefore have different scales. A recalculated risk difference, when included, is a simple unadjusted contrast based on posted summary counts; it is not a replacement for the sponsor’s own analysis.

Overall survival is also a time-to-event endpoint, but its event is death rather than progression or death. PFS and overall survival answer related but distinct questions. Response outcomes can occur earlier and are not direct substitutes for either time-to-event outcome. The registry lists other secondary measures, including duration of response, time to first response, and time to treatment failure.

General statistical interpretation: confidence intervals describe a range of effect estimates compatible with the observed data under the method’s assumptions. A narrow interval indicates greater statistical precision than a wide interval, but precision does not remove possible bias, measurement limitations, or uncertainty about whether the analysis assumptions hold.

11. Confidence Intervals and Precision

The 95% confidence intervals quantify uncertainty around the reported estimates under the analysis methods. For the primary comparison of the until-progression lenalidomide regimen with MPT, the hazard ratio was 0.72 and its interval was 0.61 to 0.85. For the comparison with Rd18, the estimate was 0.70 and the interval was 0.60 to 0.82. Both intervals lie below 1, the reference value for equal hazards. For Rd18 versus MPT, the estimate was 1.03 and the interval was 0.89 to 1.20; this interval includes 1 and permits effects in either direction.

The PFS median estimates also have confidence intervals. For the until-progression group, the median was 25.5 months with an interval from 20.7 to 29.4 months. For Rd18, it was 20.7 months with an interval from 19.4 to 22.0 months; for MPT, it was 21.2 months with an interval from 19.3 to 23.2 months. These are intervals for each group’s median estimate, not direct intervals for the difference between group medians. The reported hazard-ratio intervals address the pairwise time-to-event comparisons on a different scale.

The final overall survival intervals are also not equally narrow across all groups: the reported median estimates range from 49.1 months to 62.3 months, with intervals of different widths. A confidence interval is not a guarantee that the true value lies within its endpoints, nor does overlap or non-overlap of separate group intervals replace a direct comparison test. The registry’s pairwise hazard ratios and their intervals are the relevant reported comparative summaries.

Precision reflects statistical uncertainty under the analysis, not every source of uncertainty. Open-label conduct, endpoint assessment, censoring, missing assessments, and unreported analysis details may affect interpretation in ways that confidence intervals alone do not capture.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on observed effects, not the original trial’s design justification. For time-to-event comparisons, the figures are total event counts, not participants per arm. For binary 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. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the illustrative number of required events or participants under which a test would have an 80% chance of detecting the specified effect if that effect were true and the assumptions held. The 90% power column gives the corresponding target for a 90% chance. These are design-planning probabilities, not probabilities that the observed result is correct. Smaller effects are harder to distinguish from random variation, so the planning scenarios for a smaller fraction of the observed effect require more events or participants.

These figures are not observed power. They should not be read as evidence that the completed trial was adequately or inadequately powered, because the registry record does not report the original sample-size justification or full original design assumptions. The trial’s actual randomized group sizes and observed event counts are separate from these illustrative targets.

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 = 0.720, so ln(HR) = -0.3285.
2. d = 4 × (1.96 + 0.842)² / [ln(0.720)]² = 290.9, rounded up to 291 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 <- 0.72                              # 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(689936)
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 = 291 (80% power), 390 (90% power)
 75% of observed effect: events = 518 (80% power), 693 (90% power)
 50% of observed effect: events = 1,164 (80% power), 1,558 (90% power)
Simulated power with 291 events: 0.790 (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 645 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 1,623 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 <- 21.2          # control-arm median, months (converted from the posted unit)
hr          <- 0.72          # 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: 570         p (1-sided)   0.0001
 Events: 132        ~HR at bound   0.5231
   Month: 21    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.72   0.0338
   IA 2: 67%                   Z   2.5114
      N: 646         p (1-sided)   0.0060
 Events: 263        ~HR at bound   0.7333
   Month: 34    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.72   0.5603
       Final                   Z   1.9930
      N: 646         p (1-sided)   0.0231
 Events: 394        ~HR at bound   0.8179
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.72   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 time-to-event comparisons in the registry are sponsor-reported hazard ratios with log-rank p-values. The statistical summaries use those reported estimates rather than recalculating hazard ratios from median PFS or overall survival. Medians alone do not contain the event-time information needed to reproduce a hazard ratio or a log-rank test.

For binary response outcomes, the sponsor’s reported analyses use Fisher exact tests and odds ratios. Any displayed unadjusted recalculation from response counts is a separate summary based on posted aggregate numbers; it does not replace the sponsor’s analysis or account for unreported adjustments. The sponsor-reported estimates should be treated as the primary record of the trial’s own analyses.

No discrepancy is flagged between the posted summaries and the recalculation approach used for these comparisons. That does not mean every analysis detail can be independently checked: individual-level data, the full statistical analysis plan, and details of all modeling decisions are not reported in the registry record. Interpret the sponsor analyses as reported, while recognizing that the public summaries do not permit a complete independent reanalysis.

16. Multiplicity, Missing Data and Analysis Populations

The registry lists 45 outcome measures and 54 analyses, including a primary PFS endpoint and multiple secondary outcomes. The reported analyses include several pairwise comparisons among the three randomized groups, along with different types of outcomes and assessments. When many hypotheses are tested, the chance of obtaining at least one small p-value by chance can be greater than for a single prespecified test. Adjustments, hierarchical testing, or other strategies can address this issue, but the registry record does not report whether any such multiplicity strategy was planned or used.

The original statistical analysis plan, the prespecified hypothesis hierarchy, and the treatment of all secondary comparisons are not reported in the registry record. It is therefore not possible to determine from the record whether each listed analysis was confirmatory, whether endpoints were selected after results were known, or how any planned testing sequence was applied. The reported p-values should be read as the values attached to the stated analyses, not as evidence that multiplicity has been addressed.

The primary population is described as ITT: all randomized participants, regardless of whether they received study treatment. That is an important definition, but the registry does not give a complete participant flow or detailed analysis-population counts for every endpoint. The PFS description specifies censoring in several circumstances, including withdrawals, new anti-myeloma treatment before documented progression, and certain assessment gaps. The number of participants affected by each situation and the results of sensitivity analyses are not reported in the registry record.

General statistical context: missing assessments and censoring are not automatically equivalent to missing completely at random. Their impact depends on why observations are unavailable and whether those reasons relate to outcome or treatment. The posted description gives rules for censoring but not enough detail to assess all such possibilities. No further assumptions about missing-data handling or interim analyses can be established from 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 (11.3%), anaemia (4.5%), pyrexia (4.1%), back pain (4.1%), renal failure acute (3.9%).

The registry reports participants with serious adverse events in each treatment group as counts alongside the number at risk: 378 of 532 for the until-progression lenalidomide regimen, 308 of 540 for Rd18, and 270 of 541 for MPT. It also reports participants affected by other adverse events as 523 of 532, 532 of 540, and 532 of 541, respectively. These are recorded counts, not adjusted comparisons of safety between groups. The registry excerpt does not give a comparative statistical analysis for these figures.

The most frequently listed serious adverse event terms include pneumonia (11.3%), anaemia (4.5%), pyrexia (4.1%), back pain (4.1%), acute renal failure (3.9%), and pulmonary embolism (3.8%). The listed terms are not accompanied by arm-specific percentages, so they should not be attributed to a particular treatment group. Death counts are not reported in the registry record. The serious-event totals describe reported safety events during the study and should be interpreted with the trial’s treatment schedules and follow-up context in mind; they do not by themselves establish comparative causality.

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

The posted primary results describe differences in estimated progression-free survival across the randomized groups. In the reported pairwise analyses, the until-progression lenalidomide regimen had a hazard ratio below 1 compared with both MPT and the 18-cycle lenalidomide regimen, and the reported confidence intervals for those comparisons were below 1. The Rd18-to-MPT estimate was close to 1, with a confidence interval that included 1. These are statistical comparisons of group outcomes under the trial’s endpoint definitions and follow-up, not statements about what will happen to any individual participant.

The record also reports overall survival and response outcomes. They provide complementary evidence, but they are not interchangeable with PFS. The trial was open-label, and the primary endpoint relied on IRAC review while some response outcomes were based on investigator assessment. The available summaries do not establish that all potential sources of bias or uncertainty were eliminated.

A hazard ratio is a relative time-to-event comparison, not a percentage reduction in an individual’s risk and not a guarantee of longer survival for every participant. A median summarizes a distribution rather than describing each person’s experience. Confidence intervals convey sampling uncertainty under the analysis assumptions; they do not incorporate every limitation of the study or prove that a treatment effect is clinically important.

The registry record does not report the original sample-size justification, a complete statistical analysis plan, or a multiplicity strategy. The reported outcomes therefore support interpretation of the analyses as posted, while leaving unanswered questions about design decisions and the role of secondary tests. These results should be understood as evidence from one randomized trial in its stated population and setting, not as medical advice or a prediction for an individual.

19. Why This Trial Matters Statistically

This trial is statistically informative because it directly compares three treatment strategies rather than only two. The two lenalidomide-and-dexamethasone groups differ in the planned duration of treatment, while MPT provides a distinct active comparison. Pairwise results can therefore address both comparisons with MPT and the comparison between treatment schedules, though each contrast has its own estimate and uncertainty.

The primary outcome uses time-to-event methods, which retain information about when progression or death occurred and allow follow-up to vary across participants through censoring. This makes careful endpoint definitions and censoring rules central to interpretation. The registry identifies the ITT population and describes the main PFS event and several censoring situations, allowing readers to understand the broad analytic framework even though the full analysis plan is unavailable.

The record also illustrates why statistical significance, effect size, and precision need to be considered together. Hazard ratios and confidence intervals convey relative effects and uncertainty, while median estimates describe each group’s event-time distribution. A small p-value alone does not describe the magnitude or practical meaning of a difference. Likewise, a nonsignificant comparison does not establish equivalence.

Finally, the collection of secondary outcomes shows how a trial can examine disease response, duration, and survival from different angles. Those outcomes can enrich the interpretation but raise multiplicity concerns when many analyses are reported without a documented adjustment plan. The distinction between a designated primary result and secondary evidence is therefore important for a disciplined reading of the record.

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 contains aggregate summaries rather than individual participant data. It therefore does not allow independent reconstruction of Kaplan-Meier curves, log-rank tests, hazard ratios, or censoring decisions. The original sample-size justification and full statistical analysis plan are not reported, limiting assessment of how the trial was designed to detect differences and how analysis choices were prespecified.

The study was open-label. The primary PFS assessment was based on IRAC review, but the registry does not give enough detail to assess the review procedures or possible differences in assessment timing. Some secondary response outcomes were investigator-assessed. The record also specifies censoring rules for PFS but does not quantify how many participants were affected by each rule or report sensitivity analyses addressing alternative handling.

The number of listed outcome measures and analyses makes multiplicity relevant; a planned correction or hierarchy is not reported. The available record also does not provide a full participant flow, arm-specific serious adverse event terms, or death counts for the safety summary. Those omissions restrict comparisons across outcomes and groups.

These limitations do not invalidate the reported estimates, but they set boundaries on what can be concluded from public registry summaries alone. In particular, uncertainty intervals describe sampling uncertainty under the methods used, not the effects of unreported analytic choices, incomplete outcome ascertainment, or possible bias.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study to Determine Efficacy and Safety of Lenalidomide Plus Low-dose Dexamethasone Versus Melphalan, Prednisone, Thalidomide in Patients With Previously Untreated Multiple Myeloma — NCT00689936.
• Registry record last updated 2019-11-20; status last verified 2019-11.
• Results first posted 2017-08-11.
• 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

NCT00689936 is a completed, randomized, open-label, parallel-group phase III study with 1623 participants with previously untreated multiple myeloma. It compared lenalidomide plus low-dose dexamethasone until disease progression, the same combination for 18 four-week cycles, and MPT for 12 six-week cycles. The primary endpoint was IRAC-assessed PFS, defined by progression or death.

The registry reports longer estimated PFS medians for the until-progression lenalidomide group than for the other groups, with reported hazard-ratio comparisons favoring that group over MPT and Rd18. The Rd18-versus-MPT estimate was close to 1. Overall survival and response were among the secondary outcomes. The registry does not report the original sample-size justification, full statistical analysis plan, or multiplicity strategy.