Lenalidomide and Dexamethasone With/Without Stem Cell Transplant in Patients With Multiple Myeloma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lenalidomide and Dexamethasone With/Without Stem Cell Transplant in Patients With Multiple Myeloma (NCT01731886), a randomized phase 4 study. The primary outcome is Complete Response Rate.

2. Clinical Question

The trial’s stated objective was to compare response to the treatment combinations and their side effects. The primary endpoint is a response measure, while overall survival and progression-free survival are listed as secondary outcomes. These outcomes describe different aspects of the trial: response records a category of disease response, whereas the secondary outcomes concern survival status over a stated follow-up period.

The main comparison is between two treatment strategies, not a comparison of transplant with no other therapy. Both arms include lenalidomide and low-dose dexamethasone; the distinction in the registry descriptions is whether transplant follows treatment in Arm A. The posted data should therefore be interpreted as a comparison of the assigned strategies as recorded, rather than as an isolated estimate of the effect of transplant apart from the accompanying treatment and timing.

3. Trial Design

The registry identifies this as a phase 4, randomized, parallel-group study with no masking. Columbia University is listed as sponsor, and the condition is multiple myeloma. The status is completed. The registry gives a start date of 2012-09 and a primary completion date of 2017-04-11.

The planned comparison assigned participants to Arm A, lenalidomide and low-dose dexamethasone followed by autologous peripheral blood stem cell transplant, or Arm B, lenalidomide and low-dose dexamethasone without transplant. The arm descriptions mention stem cell collection in both strategies. The registry also lists melphalan, G-CSF, cyclophosphamide, and Mesna among the interventions. The available arm descriptions are truncated, so they do not give a complete account of the treatment schedules or all procedures.

Random allocation is intended, in general, to make treatment groups comparable on average with respect to factors that could affect outcomes. It does not guarantee that the groups will be alike in a particular trial, especially when the posted arm counts are limited. No masking means the registry describes the study as unblinded; it does not report a masked assessment process for the primary outcome.

The registry enrollment is 60. The primary endpoint data list 31 participants in Arm A and 28 in Arm B, and the primary endpoint description notes that 1 participant in Arm B never started treatment. These figures should be read as the record presents them; they do not by themselves explain the difference between enrollment and the endpoint counts. The registry does not report the original sample-size justification, the intended analysis population, or the 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 1 participant in Arm B never started treatment.

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 Complete Response Rate, measured over 3 years.

The primary endpoint is complete response rate at 3 years. The registry defines the response category to include unconfirmed complete response, complete response, and stringent complete response. In the posted results it is expressed as a count of participants, rather than as a time-to-event measure or a continuous laboratory value.

A response endpoint is used to describe whether participants meet a prespecified response category during the relevant assessment period. It addresses a different question from survival: a participant can meet a response definition without that endpoint itself establishing how long the response lasts or what happens later. The registry lists overall survival and progression-free survival separately as secondary outcomes.

The results report 7 participants with the endpoint in Arm A, among 31 listed, and 7 in Arm B, among 28 listed. The record notes that 1 participant in Arm B never started treatment. It does not explain in detail how this participant was handled in the primary analysis, whether response assessments were missing for other participants, or whether the analysis followed an intention-to-treat principle. Those details matter because the choice of analysis population and the handling of absent assessments can affect the interpretation of a response rate.

The endpoint is clinically interpretable as a response classification, but the registry record does not report the assessment schedule, the criteria used to classify response, or the method used to confirm response. Those details, as well as the original analysis plan, are not reported in the registry record.

7. Results Posted in the Registry

• Arm B: Low-dose Dexamethasone: 25.0% (7/28) versus 22.6% (7/31) on control; risk difference 2.4 percentage points (95% CI -19.3 to 24.2), risk ratio 1.11 (0.44–2.76); unadjusted two-proportion z-test p = 0.827.

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 Rate (OS)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Low-dose Dexamethasone: 78.9% (15/19) versus 80.0% (20/25) on control; risk difference -1.1 percentage points (95% CI -25.2 to 23.1), risk ratio 0.99 (0.73–1.34); unadjusted two-proportion z-test p = 0.932.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Low-dose Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

Progression Free Survival (PFS)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: Low-dose Dexamethasone: 31.6% (6/19) versus 36.0% (9/25) on control; risk difference -4.4 percentage points (95% CI -32.5 to 23.7), risk ratio 0.88 (0.38–2.04); unadjusted two-proportion z-test p = 0.759.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B: Low-dose Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide a related but distinct view from the primary complete response endpoint. Overall survival and progression-free survival are reported at 4 years, while the primary response endpoint is specified at 3 years. The secondary estimates point in different directions in their arm-to-arm comparisons, and their uncertainty intervals are broad and include zero. Taken together, they do not create a consistent, precise pattern of separation between the strategies.

These findings do not overturn or independently confirm the primary result. Response, overall survival, and progression-free survival measure different outcomes over different time frames. Similarity or difference in one cannot be assumed to imply the same result in another. The primary result itself is also imprecise, so the secondary endpoints should be read as additional descriptive information rather than a resolution of uncertainty about the primary question.

The registry lists the secondary outcomes but reports no analyses for them. The effect comparisons in the posted results are unadjusted recalculations from summary data. When multiple outcomes are examined, the chance of finding an apparently notable result by chance can increase; methods for controlling that issue depend on the prespecified analysis plan. The registry record does not report a multiplicity procedure, hierarchy of outcomes, or confirmatory status for the secondary endpoints.

Survival percentages at a fixed follow-up point also do not provide the full time course of events. The record does not report event-time data, censoring details, or a time-to-event analysis for these results. Accordingly, the secondary outcomes are useful for describing what the registry posts, but they should carry less inferential weight than a fully specified, prespecified analysis with a reported method and appropriate consideration of multiplicity.

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

• Overall Survival Rate (OS)
• Overall Survival Rate (OS)
• Progression Free Survival (PFS)
• Progression Free Survival (PFS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is a binary-outcome comparison: each participant either met the complete response definition or did not, as represented in the posted count. A risk is the proportion of participants with the outcome in an arm. A risk difference compares those proportions by subtraction; its zero value corresponds to equal observed risks. The posted comparison is oriented as Arm B relative to Arm A. The estimate of 0.024 is therefore a small positive difference on that scale, but the confidence interval is broad and includes zero.

What does the confidence interval describe?

A confidence interval describes statistical uncertainty around an estimate under the assumptions of the method used. In repeated studies conducted under the same conditions, the interval-producing procedure would capture the underlying quantity at its stated confidence level at the corresponding frequency. It is not a guarantee that the true difference lies inside this particular interval, and it is not a range of outcomes for individual participants. Here, the primary interval runs from -0.194 to 0.242. Its width indicates that the posted primary data allow a broad range of possible differences.

How should the p-value be read?

A p-value evaluates how incompatible the observed data are with a specified null hypothesis, under the assumptions of the test. The primary unadjusted p-value is 0.827. It does not give the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. A result that is not statistically significant does not establish that the treatments are equivalent. That conclusion would require a suitable design, a prespecified equivalence or noninferiority margin, and an analysis intended to address it; these are not reported in the registry record.

The same cautions apply to the posted secondary comparisons. Their p-values are unadjusted, and the confidence intervals for both risk differences include zero. For secondary outcomes, an unadjusted p-value does not account for the fact that more than one outcome may be examined. The registry lists overall survival and progression-free survival, each with repeated entries in the outcomes list, but the record does not state how many comparisons were planned or how their interpretation was to be controlled.

Why does the analysis population matter?

In a randomized trial, an intention-to-treat analysis generally compares participants according to their randomized assignment, regardless of whether they began or completed the assigned treatment. Other approaches can restrict analysis to participants who started treatment or had an outcome assessment. These approaches answer different questions and can be affected differently by treatment discontinuation, non-start, or missing outcome data. The record says that 1 participant in Arm B never started treatment, but it does not state how that participant was included in the primary endpoint analysis. The analysis population and rules for missing data are not reported in the registry record.

The registry gives a primary outcome count and group size, but not the assessment process behind those results. It does not report the response criteria, the timing of response assessments, whether assessors were blinded, or how unconfirmed responses were handled beyond their inclusion in the endpoint definition. Without these details, the count can be described, but the method of establishing the response category cannot be independently evaluated from the registry record alone.

What does randomization contribute?

Randomization is a design method intended to reduce systematic differences between groups at the time of assignment. It can support causal interpretation when the allocation is implemented as intended and when follow-up, outcome measurement, and analysis preserve the comparison. Randomization does not remove uncertainty due to limited outcome information, missing data, or chance imbalances. The registry identifies randomized allocation but does not report the allocation sequence method, concealment procedure, or stratification factors.

The study is listed as having no masking. In general, lack of masking can matter if knowledge of treatment assignment affects care, participant reporting, assessment, or decisions about follow-up. Whether those pathways influenced this trial cannot be determined from the registry record. The record does not report blinded outcome assessment or procedures intended to limit assessment bias.

What do the survival percentages represent?

The posted overall survival and progression-free survival results are percentages at 4 years, accompanied by 95% confidence intervals. The registry reports no analyses for these outcomes. The recalculated comparisons treat the posted values as binary outcomes at the specified follow-up time; they are not a reconstruction of a time-to-event model. A time-to-event analysis can use the timing of events and account for censoring, whereas a percentage at a stated time point does not show those details on its own. The registry record does not provide event-time data, censoring information, or a reported survival-analysis method.

In general, over-dispersion is a concern when observed variability exceeds what a simple model assumes, and it can make standard errors too small if ignored. It is not possible to assess over-dispersion from the posted binary endpoint counts alone, and the record does not report a model that would allow it to be evaluated. The results should not be attributed to a more complex model than the registry documents.

All comparisons described as recalculated are simple, unadjusted calculations from the posted summary statistics. No adjusted effect estimates or sponsor-reported statistical tests are listed in the record. Since the discrepancy indicator is false, no mismatch with a sponsor analysis is identified; if sponsor analyses were available, they would remain the primary reference for the sponsor’s prespecified inference. The registry does not report that analysis plan, interim analyses, or any adjustment for multiple comparisons.

11. Confidence Intervals and Precision

Precision is the amount of uncertainty around an estimate. A confidence interval gives more information about precision than a point estimate alone: a narrow interval indicates a more tightly estimated quantity, while a wide interval leaves more possible values compatible with the data and method. The primary risk-difference estimate is 0.024, but its 95% confidence interval extends from -0.194 to 0.242. The interval includes zero, so the posted data are compatible with no difference as well as differences in either direction.

The same broad uncertainty appears in the secondary comparisons. The four-year overall survival risk-difference interval is -0.252 to 0.231, and the progression-free survival interval is -0.325 to 0.237. Both include zero and span substantial differences in either direction. The point estimates alone should not be read as precise measures of the relative performance of the strategies.

For the secondary outcomes, the arm-specific 95% confidence intervals also show uncertainty: overall survival is 79.8% with an interval of 64.0% to 95.6% in Arm A, and 78.9% with an interval of 60.6% to 97.3% in Arm B. Progression-free survival is 36.0% with an interval of 17.2% to 54.8% in Arm A, and 31.6% with an interval of 10.7% to 52.5% in Arm B. The intervals overlap, but overlap alone is not a formal test of the difference; the risk-difference intervals are the direct uncertainty summaries for the posted comparisons.

Confidence intervals do not account for every possible source of uncertainty. They depend on the calculation method and do not resolve questions about missing outcomes, measurement, analysis-population choices, or multiple comparisons. Those procedures are not reported in the registry record. The displayed precision should therefore be understood as statistical uncertainty under the recalculation, not as a complete account of all uncertainty in the trial.

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 the observed effect, not the original trial design assumptions. For these binary outcomes, the figures refer to participants per arm. The 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 as the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size justification or original design assumptions.

The 80% power column indicates the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect if that effect were the true one, under the listed calculation assumptions. The 90% power column gives the corresponding planning target for a 90% chance. These are design calculations, not descriptions of what happened in the completed trial. They should not be confused with the trial’s enrollment or endpoint group counts.

Rows planning for 75% or 50% of the observed effect use smaller target effects than the row planning for 100% of the observed effect. Smaller effects are harder to distinguish from chance variation, so they require more participants per arm for the same power target. The figures are particularly sensitive to the observed effect used as their starting point: an estimate from a limited dataset can be unstable, and a near-zero estimate can make such illustrations uninformative as a practical design target.

The sample-size planning estimates are not observed power. Observed power would not add a reliable interpretation of the completed trial beyond the effect estimate and its uncertainty. The useful reading is prospective: under the stated assumptions, what group size would be needed to detect a chosen effect with the specified power? The registry record does not report whether these assumptions match the investigators’ original plans.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.226; treatment proportion p₁ = 0.250; average p̄ = 0.238.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6022 = 1.1802.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6019 = 0.5066.
4. n = (1.1802 + 0.5066)² / (0.0242)² = 4,861.2, rounded up to 4,862 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 <- 0.225806451612903                          # control proportion
p1 <- 0.25                          # 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(1731886)
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 = 4,862 (80% power), 6,508 (90% power)
 75% of observed effect: n per arm = 8,568 (80% power), 11,469 (90% power)
 50% of observed effect: n per arm = 19,105 (80% power), 25,575 (90% power)
power.prop.test: 4861.2 
Simulated power at n = 4,862 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses more than one outcome, comparison, or analysis. Each additional test creates another opportunity for a result to appear statistically notable by chance. Statistical plans can address this through a prespecified hierarchy, adjustment procedure, or clearly designated exploratory analyses. The registry record lists complete response as the primary endpoint and lists overall survival and progression-free survival as secondary outcomes, but it does not report how multiplicity was handled.

The posted secondary comparisons are unadjusted. Their p-values should therefore be interpreted as individual, unadjusted comparisons, not as values adjusted for the number of outcomes examined. The record does not state whether the secondary endpoints were confirmatory or exploratory, whether there were additional planned analyses, or whether any outcome hierarchy was used. Without that information, the secondary results have less evidential weight than a prespecified primary analysis and should not be treated as independent confirmation.

Missing-data handling is another unresolved issue. The primary endpoint description notes that 1 participant in Arm B never started treatment. The record does not say whether that participant was included in the primary analysis, how absent response assessments were classified, or whether any imputation or sensitivity analysis was used. It also does not report missingness information for the secondary outcomes.

The analysis populations are not described. The registry does not identify whether the primary comparison used all randomized participants, those who started treatment, those with an available assessment, or another population. These choices can affect an estimate, especially if missingness or treatment initiation differs between arms. The registry also does not report a protocol deviation analysis or sensitivity analyses addressing these choices.

The record contains no reported analyses for the secondary outcomes and does not give the complete statistical analysis plan. Details of interim analyses, sample-size justification, allocation concealment, and any prespecified model are not reported in the registry record. These absences limit assessment of whether the posted comparisons correspond to the investigators’ intended analyses.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: presyncope (3.6%), bone pain (3.6%), infection with grade 3 or 4 neutrophils (3.6%), infection (3.6%), myelodysplastic syndrome (3.6%).

The registry reports serious adverse events in 7 of 31 participants in Arm A and 7 of 28 in Arm B. It also reports other, non-serious adverse events in 21 of 31 in Arm A and 19 of 28 in Arm B. The counts describe participants with reported events within the listed at-risk groups; they do not establish that an event was caused by a study treatment.

The record lists deaths in 14 participants in Arm A and 11 in Arm B. These are posted death counts and should not be interpreted as treatment-related deaths without information about attribution, timing, follow-up, and the definitions used. The registry does not provide a causal analysis of these deaths in the registry record reported for this comparison.

Among the listed serious adverse event terms, Presyncope, Bone Pain, Infection with Grade 3 or 4 Neutrophils, Infection, Myelodysplastic Syndrome, and Pain of skin are each reported at 3.6%. The record’s summary does not establish whether these terms are exhaustive, how events were grouped, or how their severity and relatedness were assessed. Safety counts are descriptive and should be read alongside the definitions and follow-up procedures, which are not reported in the registry record.

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

The results describe a randomized comparison of two treatment strategies for newly diagnosed multiple myeloma, with a primary endpoint based on complete response at 3 years. The posted counts are 7 in each arm. The unadjusted risk-difference estimate is small and positive for Arm B relative to Arm A, but its confidence interval is broad and includes zero. The primary comparison therefore leaves substantial uncertainty about the direction and size of any difference.

That uncertainty is not evidence that the strategies are identical. A finding of equivalence would require an explicit margin and an appropriate design and analysis, none of which is reported in the registry record. Nor does the posted result establish that one strategy is superior. The estimate and interval describe what can be inferred from the available summary data under the calculation method, not a definitive treatment conclusion.

The secondary survival outcomes are also imprecise. Their fixed-time estimates and risk-difference intervals do not show a precise separation, and the registry provides no reported analyses for those endpoints. Because they are secondary, unadjusted comparisons and have different definitions and follow-up from the primary outcome, they cannot substitute for a prespecified primary analysis or settle the uncertainty in it.

The trial is listed as randomized, which is a strength for comparing assigned strategies in principle. However, the registry identifies no masking and does not report the analysis population, missing-data rules, detailed response assessment methods, or multiplicity procedure. The primary outcome description notes a participant in Arm B who never started treatment, but the record does not explain how this was handled analytically.

These registry results support a cautious statistical reading: the posted data are compatible with a range of outcomes, and they do not provide a precise estimate of comparative effects. They do not by themselves establish causal effects beyond the trial’s reported design and analysis details, and they are not medical advice. Treatment choices require clinical judgment and information beyond these summary statistics.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it illustrates the difference between an estimated effect and the certainty surrounding it. The primary point estimate is easy to state, but its confidence interval is wide enough to include no difference and differences in either direction. Readers who focus only on the point estimate or the p-value miss the central limitation: the posted data do not pin down the comparative response rate with precision.

It also shows why a non-significant result is not an equivalence result. A failure to reject a null hypothesis does not demonstrate that two strategies have the same outcome. That requires a planned equivalence or noninferiority question, an appropriate margin, and analysis methods suited to that purpose. The registry record does not report those elements.

The contrast between the primary response endpoint and the secondary survival outcomes is another useful lesson. These outcomes address different questions, use different follow-up time frames, and have their own uncertainty. Multiple unadjusted endpoints can be informative descriptively, but they should not be treated as a collection of independent confirmatory tests. The record does not say how multiplicity was handled.

Finally, transparent interpretation depends on more than randomized allocation and arm-level counts. Analysis populations, missing-data rules, assessment methods, and prespecified analysis plans help readers understand how results were produced and what claims they support. Those details are not reported in the registry record. The case therefore highlights the value of reading effect estimates together with their uncertainty and the methodological context available.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves important trial-specific details unresolved. Although it identifies randomized allocation and no masking, it does not report how the allocation sequence was generated or concealed, whether allocation was stratified, or whether outcome assessment was blinded. These omissions limit evaluation of how well the assigned comparison was protected from selection or assessment bias.

The arm descriptions are truncated. They identify the broad treatment strategies and some cycle and collection details, but do not provide complete regimens or schedules. The registry lists several interventions, including melphalan, G-CSF, cyclophosphamide, and Mesna, without enough detail in the posted arm text to characterize their precise use across groups.

The response assessment criteria and timing are not reported beyond the primary endpoint timeframe and the inclusion of unconfirmed complete response, complete response, and stringent complete response. The record does not explain adjudication, confirmation rules, or handling of absent assessments. It notes that 1 participant in Arm B never started treatment but does not specify the analytic treatment of that participant.

The original sample-size justification and statistical analysis plan are not reported. The registry does not provide the intended analysis population, missing-data methods, interim-analysis plan, or multiplicity adjustment. Secondary outcomes have no reported analyses, and the posted comparisons are unadjusted recalculations rather than a reported time-to-event analysis. The registry also does not provide event-time or censoring details for the survival percentages.

Finally, the posted safety summary does not include enough detail to assess event attribution, timing, duration, or the completeness of event reporting. These limitations do not invalidate the recorded counts, but they restrict what can be concluded from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Lenalidomide and Dexamethasone With/Without Stem Cell Transplant in Patients With Multiple Myeloma — NCT01731886.
• Registry record last updated 2020-02-05; status last verified 2020-01.
• Results first posted 2019-10-15.
• 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.

22. Record Summary

The registry describes a completed, randomized, open-label, parallel-group phase 4 trial sponsored by Columbia University. It compares lenalidomide and low-dose dexamethasone followed by autologous peripheral blood stem cell transplant with lenalidomide and low-dose dexamethasone without transplant in newly diagnosed multiple myeloma.

The primary endpoint is complete response at 3 years, including unconfirmed complete response, complete response, and stringent complete response. The posted counts are 7 of 31 in Arm A and 7 of 28 in Arm B; the record notes that 1 participant in Arm B never started treatment. The unadjusted comparison is imprecise, with a risk difference of 0.024 and a 95% confidence interval from -0.194 to 0.242.

Overall survival and progression-free survival are listed at 4 years as secondary outcomes. Their posted estimates and unadjusted comparisons are also uncertain. The registry does not report secondary analyses, the original sample-size rationale, detailed analysis populations, or key missing-data and multiplicity procedures. The results are best read as descriptive evidence with substantial uncertainty.