Lenalidomide (Revlimid®) Plus Low-dose Dexamethasone (Ld x 4 Cycles) Then Stem Cell Collection Followed by Randomization to Continued Ld or Stem Cell Transplantation (SCT) Plus Maintenance L: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lenalidomide (Revlimid®) Plus Low-dose Dexamethasone (Ld x 4 Cycles) Then Stem Cell Collection Followed by Randomization to Continued Ld or Stem Cell Transplantation (SCT) Plus Maintenance L (NCT00807599), a randomized phase 2 study. The primary outcome is Progression Free Survival (PFS) Rate at 2 Years After Enrollment in Untreated Patients With Multiple Myeloma..

2. Clinical Question

The clinical question is about outcomes following two treatment strategies in transplant-eligible patients with untreated, standard-risk symptomatic multiple myeloma. It is not a comparison of completely separate treatments from the outset: both groups first received lenalidomide and dexamethasone and underwent stem cell collection. Randomization then separated the strategies of continuing lenalidomide and dexamethasone or proceeding to stem cell transplant. The record describes transplantation as one or two procedures but does not report how that choice was determined.

The primary endpoint is a rate at a specified time after enrollment, rather than a reported comparison of the entire time-to-event experience. The registry lists a 2-year progression-free survival rate of 84.6% for continued lenalidomide and dexamethasone and 83.3% for stem cell transplant. The interpretation depends on the accompanying uncertainty: the confidence intervals are wide and overlap substantially. The registry does not report the outcome definition in further detail, the handling of censoring, or an analysis population definition, so the clinical question can be described more clearly than the exact statistical procedures used to answer it.

3. Trial Design

This was a phase II, randomized, parallel-group study with no masking. It enrolled 67 patients with multiple myeloma and is recorded as completed. The sponsor was Memorial Sloan Kettering Cancer Center. The registry lists a study start date of 2008-12-10 and a primary completion date of 2018-07. The registry record does not report the randomization method beyond identifying the allocation as randomized.

The treatment sequence matters when interpreting the comparison. All patients started with lenalidomide and dexamethasone by mouth. After 4 cycles and completion of stem cell collection, patients were randomized to continue lenalidomide and dexamethasone or receive stem cell transplant x 1 or x 2. Thus, the reported arm comparison concerns the strategies assigned after the common initial treatment and collection period, among patients reaching that point in the study. The registry does not report the number who began the initial treatment, completed collection, or were randomized, nor does it provide a flow of participants through these stages.

The posted arm sizes for the primary outcome are 26 for continued lenalidomide and dexamethasone and 24 for stem cell transplant. These arm-specific figures are not the same as the overall enrollment figure; the registry does not explain the difference between the enrollment count and the outcome denominators. The record does not report whether patients were analyzed according to assigned treatment, treatment received, or another analysis population.

Because the trial was unmasked, participants and clinicians were not described as unaware of assigned treatment. The registry does not report masking of outcome assessors or analysts. It also does not report the original sample-size justification, planned enrollment by arm, randomization sequence procedures, or any interim analysis plan. These omissions limit what can be said about design intent and analysis safeguards. The results are best read as the reported outcome estimates for the posted groups, with the uncertainty and incomplete methods detail kept in view.

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:

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 Progression Free Survival (PFS) Rate at 2 Years After Enrollment in Untreated Patients With Multiple Myeloma., measured over 2 years.

The primary endpoint is the progression-free survival (PFS) rate at 2 years after enrollment in untreated patients with multiple myeloma. It is reported as a percentage of participants, with a 95% confidence interval for each arm. The registry gives a rate of 84.6% (95% confidence interval 70.7% to 98.5%) for continued lenalidomide and dexamethasone, and 83.3% (95% confidence interval 68.4% to 98.2%) for stem cell transplant.

In general, progression-free survival concerns the time during which a patient remains alive without documented disease progression. A rate at a set time provides a snapshot of the estimated proportion meeting that status at that point, rather than describing every event time or the full shape of the time-to-event experience. PFS is often used in clinical trials because it captures both progression and death, events that can be important when assessing the course of a serious disease. That general rationale does not establish how this particular registry defined progression, adjudicated events, or handled incomplete follow-up.

The record does not report further details of the PFS definition, the event assessment schedule, the statistical method used to estimate the rate, or the handling of censoring. It also does not state whether the time origin or analysis population differed from the wording of the endpoint. Accordingly, the endpoint can be described as the recorded 2-year rate after enrollment, but details needed to reproduce that estimate are not reported in the registry record.

7. Results Posted in the Registry

• Stem Cell Transplant x 1 or x 2: 83.3% (20/24) versus 84.6% (22/26) on control; risk difference -1.3 percentage points (95% CI -21.6 to 19.1), risk ratio 0.98 (0.77–1.26); unadjusted two-proportion z-test p = 0.902.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry describes a binary percentage outcome: the primary result is the proportion of participants reported to be progression-free at 2 years. It gives one percentage for each randomized arm and a 95% confidence interval for each estimate. The comparison is labeled as a risk difference, with the transplant arm compared against continued lenalidomide and dexamethasone. The record does not describe the statistical procedure used to calculate the confidence intervals or the p-value.

What does a percentage estimate represent?

In general, a percentage is an estimate of the share of a group meeting a defined outcome. A percentage alone does not communicate how much uncertainty surrounds that estimate. Its precision depends in part on the amount of information available and on the outcome and estimation method. Here, the arm-specific percentages are 84.6% and 83.3%, and the outcome denominators are 26 and 24. The corresponding 95% confidence intervals extend from 70.7% to 98.5% and from 68.4% to 98.2%.

A confidence interval is a range calculated by a statistical procedure that, under its assumptions, would contain the target quantity at the stated rate over repeated use of that procedure. It is not a range of individual patient outcomes and does not mean that there is a 95% probability that the fixed true rate lies in this particular calculated interval. The interval gives an indication of the uncertainty in the estimated rate. Wide intervals indicate that the data do not pin down the rate very closely.

How should the risk difference be understood?

In general, a risk difference is the event proportion in one group minus the event proportion in another group. A value on one side of zero indicates a higher estimated proportion in the first group; a value on the other side indicates a higher estimated proportion in the second group. The registry labels its estimate as the risk difference for stem cell transplant relative to continued lenalidomide and dexamethasone. Its unadjusted confidence interval includes zero. The interval is broad, so values consistent with the posted data span different directions and magnitudes of difference. Because the exact interval limits in the comparison are reported with more decimal places than permitted for display, they are not repeated; the arm-specific rate intervals provide the displayed precision for the endpoint estimates.

In general, a risk difference is often easier to interpret clinically than a relative measure because it describes an absolute separation in proportions. It still depends on the outcome definition, follow-up time, and population analyzed. The registry does not state whether the comparison was adjusted for any baseline variables, whether the test was one-sided or two-sided, or what method produced the interval. The reported p-value is identified as unadjusted, but the record does not specify which test generated it.

What does the p-value tell the reader?

In general, a p-value is calculated under a statistical model that represents a null hypothesis, commonly a hypothesis of no difference between groups. It describes the compatibility of the observed data with that model, given the test’s assumptions. It is not an effect estimate, and it does not show how large or clinically important a difference might be. It is also not the probability that the null hypothesis is true. The reported unadjusted p-value is 0.902. Read alongside the point estimates and confidence intervals, it does not give evidence of a statistically clear separation in this comparison. It does not establish that the strategies are equivalent.

The term “unadjusted” indicates that the reported p-value is not presented as adjusted for other factors or for multiple comparisons. The registry does not report an adjusted estimate, an adjusted p-value, or a description of covariates. It also does not report whether the comparison was planned as the sole primary hypothesis or how secondary endpoints were incorporated into the analysis plan.

Why can a percentage at a time point require additional methods?

In general, PFS is a time-to-event outcome because event timing matters and some participants may not have complete follow-up by the analysis date. A rate at a specified time can be estimated using methods that account for incomplete follow-up, but the appropriate interpretation depends on how events and censoring are defined and handled. The record reports the 2-year rate but does not describe the estimator, censoring rules, or follow-up completeness. It is therefore not possible to determine from the registry record whether the percentages are simple observed proportions or estimates that account for time-to-event data.

In general, over-dispersion arises when the variation in observed outcomes is greater than expected under a model’s assumptions. It can make conventional uncertainty estimates too narrow if not addressed. There is no indication in the registry record that over-dispersion was assessed or relevant to the PFS calculation; the outcome is a percentage and the analysis method is not reported. This is a general statistical consideration, not a claim about the procedure used in this trial.

Randomization helps make the assigned groups comparable in expectation, but it does not remove uncertainty, guarantee balance in a modest study, or resolve missing-data problems. The record does not report baseline characteristics by arm or an analysis population definition. It also does not provide an accounting of missing outcomes. Those omissions limit the assessment of whether the comparison was conducted as intended and how much the result might be affected by incomplete data.

10. Confidence Intervals and Precision

The 95% confidence interval for the 2-year PFS rate in the continued lenalidomide and dexamethasone arm is 70.7% to 98.5%. For stem cell transplant, it is 68.4% to 98.2%. These ranges are wide relative to their point estimates. They indicate that the reported percentages are not highly precise estimates of the underlying rates.

The arm-specific intervals overlap substantially. Overlap is not, by itself, a formal test of whether the groups differ; a direct comparison uses an estimate of the between-arm contrast and its uncertainty. The registry reports a risk-difference comparison and an unadjusted p-value of 0.902. The comparison interval includes no difference and extends across values on either side. Together, these statistics show that the posted results do not sharply distinguish the strategies.

In general, the width of a confidence interval reflects both the amount of information and the variation assumed by the statistical method. Smaller outcome groups tend to yield less precise estimates, though the exact interval also depends on the outcome and estimation procedure. The outcome denominators are 26 and 24. The registry does not explain why the primary-outcome denominators differ from the overall enrollment, and it does not report how many participants had incomplete follow-up or how censoring was handled.

Confidence intervals should not be interpreted as a guarantee that every value inside the interval is equally plausible, nor as a measure of clinical importance. The registry does not provide a threshold for a clinically important PFS difference. The intervals therefore describe statistical precision, not whether a difference would matter to patients or clinicians. Given the breadth of the intervals and the missing analysis details, the estimates support cautious descriptive interpretation rather than a precise claim about the comparative effect.

11. Planning a Similar Trial: Sample Size

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

The sample-size calculations are planning illustrations based on the observed effect, not the trial’s original design assumptions. The registry record does not report the original sample-size justification. These calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. These are planning assumptions, not a reconstruction of the study’s design.

For planning for 100% of the observed effect, the listed figures are 12,852 participants per arm for 80% power and 17,204 participants per arm for 90% power. For planning for 75% of the observed effect, they are 22,663 participants per arm for 80% power and 30,339 participants per arm for 90% power. For planning for 50% of the observed effect, they are 50,574 participants per arm for 80% power and 67,703 participants per arm for 90% power. The figures are participants per arm, not totals across arms or total event counts.

In general, power is the probability that a planned statistical test will detect an effect of the specified size under the assumptions used for the calculation. The 80% power column represents a design targeting an 80% chance of detecting that assumed effect; the 90% power column targets a higher chance. This does not guarantee that a future study will detect an effect, since actual results depend on the true effect, data, and analysis assumptions. Smaller effects need more participants to detect with the same power under the same general planning framework. These figures are not observed power for the completed trial.

The planning counts are unusually large relative to this trial’s posted outcome groups because the calculation is tied to the observed effect. A small observed difference can imply a very large sample requirement when planning to detect a similar or smaller difference. Such an illustration should not be read as a recommendation for a new trial: the registry does not report a clinically important target effect, a refined event-rate assumption, or the original design rationale.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.846; treatment proportion p₁ = 0.833; average p̄ = 0.840.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5188 = 1.0168.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5187 = 0.4366.
4. n = (1.0168 + 0.4366)² / (-0.0128)² = 12,851.4, rounded up to 12,852 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 <- 0.846153846153846                          # control proportion
p1 <- 0.833333333333333                          # 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(807599)
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 = 12,852 (80% power), 17,204 (90% power)
 75% of observed effect: n per arm = 22,663 (80% power), 30,339 (90% power)
 50% of observed effect: n per arm = 50,574 (80% power), 67,703 (90% power)
power.prop.test: 12851.4 
Simulated power at n = 12,852 per arm: 0.802 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists three secondary outcomes: number of participants with VGPR + CR rate, overall response rates, and overall survival. It also reports 4 outcome measures, but provides no analysis entries. The methods for the primary outcome and the secondary outcomes are not detailed in the registry record. Results for the listed secondary outcomes are not reported in the available record.

Multiplicity arises when several outcomes, comparisons, or repeated tests are examined. In general, the more tests performed, the greater the chance that at least one result appears statistically unusual even if all null hypotheses are true. Prespecified approaches can control that risk or define a hierarchy of endpoints. The registry does not report whether any multiplicity adjustment was planned or used, whether secondary outcomes were confirmatory or exploratory, or how the primary and secondary questions were ordered. The posted primary-comparison p-value is described as unadjusted.

The record does not report the analysis populations used for the primary or secondary outcomes. It is therefore not possible to determine whether participants were analyzed according to randomized assignment, treatment received, or another rule. The record also does not give a participant flow, outcome completeness by arm, or reasons for missing data. These details matter because an analysis restricted to participants with observed outcomes may differ from an analysis that accounts for incomplete follow-up.

For PFS, incomplete follow-up is commonly addressed through time-to-event methods, but the registry does not report censoring definitions, the estimator, or follow-up duration by arm. It also does not report whether missing data were imputed, treated as failures, or handled by another method. No assumption about those procedures should be inferred from the reported percentages alone.

The absence of analysis entries does not establish that no analyses were conducted; it means that the registry record does not report them in the outcome-analysis information. The statistical plan, missing-data strategy, analysis population definitions, and multiplicity procedures are not reported in the registry record. These gaps make it difficult to evaluate the robustness of the posted estimates or their relationship to a prespecified analysis plan.

14. 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: infection (25.0%), treatment related secondary malignancy (25.0%), febrile neutropenia (16.7%), pneumonia (16.7%), neutrophil count decreased (11.5%).

For continued lenalidomide and dexamethasone, the registry reports serious adverse events in 17 of 26 participants at risk, other adverse events in 26 of 26, and 3 deaths. For stem cell transplant, it reports serious adverse events in 18 of 24 participants at risk, other adverse events in 24 of 24, and 5 deaths. These are descriptive counts in the posted groups. The record does not explain whether the deaths were considered treatment-related or how they relate to the adverse-event categories.

The most frequently listed serious adverse-event terms include infection and treatment related secondary malignancy, each reported as 25.0%; febrile neutropenia and pneumonia, each at 16.7%; neutrophil count decreased at 11.5%; and hemoglobin decreased at 8.3%. These terms describe event categories, not necessarily unique participants, and the record does not state whether one person could contribute to multiple terms. It also does not provide event severity grades, timing, duration, or causal attribution for these terms.

In general, safety comparisons require attention to how adverse events were collected, coded, and followed, as well as the number exposed and time at risk. Those details are not reported in the registry record. The counts should not be treated as a complete account of comparative safety or as proof that events were caused by a particular treatment.

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

The posted primary results show 2-year PFS rates of 84.6% for continued lenalidomide and dexamethasone and 83.3% for stem cell transplant. Their 95% confidence intervals are 70.7% to 98.5% and 68.4% to 98.2%. The unadjusted p-value for the comparison is 0.902. In plain terms, the point estimates are close, but the uncertainty is too broad to support a precise estimate of the difference between the strategies.

These results do not show that the treatment strategies are equivalent. A failure to demonstrate a clear difference is not the same as demonstrating that any difference is small enough to be unimportant. The registry does not report a prespecified equivalence or noninferiority margin, and the intervals allow a range of outcomes. Nor do the results establish that one strategy is better. The statistical evidence is inconclusive about comparative differences, rather than proof of sameness or superiority.

The population and sequence also constrain interpretation. Patients were described as untreated, standard-risk, symptomatic, and eligible for stem cell transplant. All began lenalidomide and dexamethasone before collection and random assignment. The findings therefore concern the assigned strategies after this shared initial stage, not every possible treatment approach or all people with multiple myeloma. The registry does not report outcomes for the secondary endpoints listed, so response and overall survival results cannot be inferred from the PFS estimate.

The adverse-event counts describe events reported in the two arms but do not establish causal relationships or provide a full comparative safety analysis. Details about exposure time, event definitions, and attribution are not reported. These results should be understood as the posted registry record, not as individualized predictions or medical advice.

Overall, the main statistical message is one of limited precision. The trial reports similar numerical PFS rates, but the outcome groups and confidence intervals do not permit a narrow estimate of the comparative effect. Further information about the analysis methods, follow-up, participant flow, and secondary outcomes would be needed for a fuller evaluation.

16. Why This Trial Matters Statistically

This trial is statistically instructive because it illustrates the distinction between a similar point estimate and a precise conclusion. The reported PFS rates are numerically close, but their confidence intervals are broad. A reader who focuses only on the percentages might conclude that the strategies produced nearly identical outcomes. The uncertainty intervals show why that conclusion would be too strong: the data do not pin down the underlying rates closely or rule out meaningful differences.

Randomized assignment is a strong feature for comparing strategies because, in general, it reduces systematic differences between groups at baseline. But randomization does not guarantee a precise result, especially when outcome denominators are limited. Nor does randomization supply missing details about analysis populations, censoring, or follow-up. Design quality and estimate precision are related but distinct considerations.

The study’s sequence is another important statistical feature. Both arms received lenalidomide and dexamethasone before assignment to the post-collection strategies. The result therefore addresses a treatment decision made after common initial therapy and stem cell collection. It should not be interpreted as a comparison of transplant against an entirely untreated or non-transplant pathway from the outset.

The registry’s unadjusted p-value is not a substitute for the effect estimate and confidence interval. A p-value can summarize compatibility with a statistical null model, but does not tell the reader whether the estimated difference is clinically important or whether the trial could rule out such a difference. The registry does not report a noninferiority or equivalence framework, so the absence of a statistically clear separation cannot establish equivalence.

Finally, the planning illustrations emphasize how sample-size requirements depend on the effect chosen for detection. Smaller target effects require more participants under the stated assumptions. Because those calculations use the observed effect and are not the original trial design, they are best treated as examples of planning sensitivity rather than a judgment on the trial’s intended size.

17. 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.

The registry record leaves several trial-specific limitations unresolved. It reports overall enrollment of 67, while the primary-outcome arm denominators are 26 and 24. No participant flow explains the difference, and the record does not say how many people began treatment, completed the initial 4 cycles, completed stem cell collection, or entered randomization. Without that flow, it is difficult to assess selection between enrollment and the posted outcome groups.

The intervention descriptions establish the shared initial treatment and the two randomized strategies, but do not provide detailed treatment schedules beyond the 4 cycles and transplant x 1 or x 2. The trial title refers to maintenance L after transplantation, but the specific maintenance regimen and its duration are not reported in the registry record. The basis for receiving one or two transplants is also not reported.

The outcome description identifies PFS at 2 years after enrollment but does not report the operational definition of progression, event review procedures, censoring rules, or the estimation method. The timing of randomization follows the common initial treatment and collection period, while the endpoint is timed from enrollment; the registry does not explain the analysis of that timing. These missing details limit reproducibility and complicate interpretation of the reported rates.

The record does not report baseline characteristics by arm, analysis populations, missing-data handling, or an original sample-size justification. It lists secondary outcomes but does not report their results in the available record. Safety reporting also lacks details about event attribution, exposure time, severity, and whether event terms represent people or occurrences. These limitations are specific gaps in the available registry information, not evidence that the procedures or data were absent from the full study record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Lenalidomide (Revlimid®) Plus Low-dose Dexamethasone (Ld x 4 Cycles) Then Stem Cell Collection Followed by Randomization to Continued Ld or Stem Cell Transplantation (SCT) Plus Maintenance L — NCT00807599.
• Registry record last updated 2019-03-15; status last verified 2018-08.
• Results first posted 2019-03-15.
• 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.

21. Record Summary

NCT00807599 is a completed phase II randomized, parallel-group trial sponsored by Memorial Sloan Kettering Cancer Center. It enrolled patients with untreated, standard-risk symptomatic multiple myeloma who were eligible for stem cell transplant. All patients began lenalidomide and dexamethasone; after 4 cycles and stem cell collection, they were assigned to continued lenalidomide and dexamethasone or stem cell transplant x 1 or x 2.

The primary endpoint was PFS rate at 2 years after enrollment. The registry reports rates of 84.6% for continued drug treatment and 83.3% for transplantation, with broad 95% confidence intervals and an unadjusted p-value of 0.902. The numerical estimates are close, but their uncertainty does not establish equivalence or rule out meaningful differences. Analysis methods, missing-data handling, participant flow, and results for the listed secondary outcomes are not reported in the registry record.