Lenalidomide and Dexamethasone With or Without Thalidomide in Treating Patients With Multiple Myeloma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lenalidomide and Dexamethasone With or Without Thalidomide in Treating Patients With Multiple Myeloma (NCT00098475), a randomized phase 3 study. The primary outcome is Proportion of Patients With Objective Response (First Phase, Step 1).

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel-group phase III study sponsored by the National Cancer Institute. The registry record lists enrollment of 452 and describes patients with DS Stage I, DS Stage II, or DS Stage III multiple myeloma. The listed study start was 2004-11-03, and primary completion was 2008-11-30. Its current registry status is active, not recruiting.

The primary endpoint concerns the first phase, Step 1: objective response with lenalidomide and standard-dose dexamethasone compared with lenalidomide and low-dose dexamethasone. The response arms list 214 participants for Arm I and 208 for Arm II. The recorded schedules differ in the dexamethasone dose and dosing days. Arm II also describes acetylsalicylic acid as part of its regimen.

The trial plan also describes thalidomide plus dexamethasone salvage treatment for patients with no response after treatment in either first-phase arm. Arm III is the standard-dose dexamethasone salvage regimen after Arm I; Arm IV is the low-dose dexamethasone salvage regimen after Arm II. Objective response in the first phase, Step 2, is listed as a secondary outcome.

The registry record notes that the expansion phase was a substudy terminated early with only 7 patients enrolled, and that the clinical results presented are mainly for the first phase. The record lists laboratory biomarker analysis among the interventions, but further details on its role are not reported in the registry record. The allocation is randomized, masking is double, and the model is parallel; details of the randomization procedure and masking implementation are not reported in the registry record.

4. Participant Flow and Accounting

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

Step 1

Reasons for not completing this period:

Step 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Only eligible patients were included in this analysis.

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 Proportion of Patients With Objective Response (First Phase, Step 1), measured over Assessed every 4 weeks for 16 weeks during Step 1.

The primary endpoint is the proportion of eligible patients with an objective response during Step 1. Objective response means either complete response or partial response. A complete response requires complete disappearance of an M-protein and no evidence of myeloma in the bone marrow. A partial response requires a reduction in serum monoclonal paraprotein of at least 50%, together with a reduction in 24-hour urinary light chain excretion of at least 90% or to under 200 mg. For patients with non-secretory or oligosecretory myeloma, the definition also requires at least a 50% reduction in plasma cells in a bone marrow aspirate and trephine biopsy. The definition additionally requires a 50% reduction in the size of soft tissue plasmacytoma and no increase in the number or size of lytic bone lesions.

The endpoint is assessed every 4 weeks for 16 weeks during Step 1. A proportion is useful for describing how often a defined response occurred within each treatment group, while the sponsor’s between-arm estimate addresses the contrast between those response rates. This endpoint does not by itself describe response duration, time to progression, survival, or the balance of benefits and harms. Those outcomes are not reported as primary results in the posted record.

7. Results Posted in the Registry

• Arm II (Lenalidomide, Low-dose Dexamethasone): 0.5% (1/208) versus 0.9% (2/214) on control; risk difference -0.5 percentage points (95% CI -2.0 to 1.1), risk ratio 0.51 (0.05–5.63); unadjusted two-proportion z-test p = 0.579.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a response proportion describe?

A response proportion is the number of participants meeting the endpoint definition relative to the participants included in that endpoint analysis. Here, response means complete or partial response according to the stated criteria, and the registry reports the proportions separately for the two Step 1 arms. Such a proportion is an absolute description of how often the defined event was recorded in the analyzed group. It is not a measure of how long response lasted, and it does not represent all aspects of disease status or safety.

The endpoint population is described as eligible patients only. That wording matters: the proportions do not necessarily use every person enrolled or every person assigned to an arm. The response arm counts and the safety denominators are reported separately, and should not be assumed to refer to identical analysis populations. The registry record does not report a detailed participant flow or explain the differences among enrollment, response-analysis counts, and safety denominators.

How should the sponsor’s contrast be read?

The sponsor’s reported quantity is the difference in response rate between arms, stated as 0.107. A difference compares two proportions on an absolute scale: it indicates the distance between the rates as expressed by the analysis. Unlike a ratio, it does not describe a proportional increase or decrease. The reported 80% confidence interval, 0.052 to 0.162, expresses the uncertainty around this contrast under the sponsor’s analysis. A confidence interval is not a guarantee that the true value falls inside its limits; it is a procedure with a stated long-run coverage property when its assumptions hold.

The sponsor’s result is recorded as a legacy non-inferiority or equivalence analysis, but the method field is not specified. The registry record does not report the margin, the formal decision rule, or a p-value for that comparison. Without those details, the label alone is not enough to reconstruct or independently assess the intended hypothesis test. The confidence interval can be described as posted, but its role in a formal non-inferiority conclusion cannot be determined from the registry record.

What is an unadjusted recalculation?

An unadjusted recalculation uses the posted summary counts and denominators to produce a simple comparison, without adjustment for other characteristics. It is distinct from a sponsor analysis that may use a prespecified model or other procedures, though the sponsor’s method is not reported. The separate recalculation in the record is a risk difference of -0.004 with a 95% confidence interval from -0.021 to 0.011 and p = 0.579. It is based on counts of 2 and 1, rather than the response proportions posted for Step 1. It therefore should not be substituted for the sponsor’s primary response-rate contrast. The record does not identify the clinical outcome represented by those counts.

A p-value summarizes how unusual data at least as inconsistent with a specified null hypothesis would be under that hypothesis and the analysis assumptions. It does not measure the probability that the null hypothesis is true, the size of an effect, or the importance of a result. The recalculated p-value belongs to its own count-based comparison and should not be attributed to the sponsor’s reported response analysis.

Why can over-dispersion matter?

In general, a binomial model assumes that each participant contributes an event or non-event and that the probability of the event is appropriately represented by the model. Over-dispersion means the observed variation is greater than the model allows. When that occurs, standard errors may be too small and confidence intervals too narrow if the extra variation is ignored. This is a general statistical consideration, not a claim that over-dispersion was present or that a particular binomial model was used in this trial; the sponsor’s method is not reported in the registry record.

What analysis details are not available?

The registry record does not report whether the primary analysis followed an intention-to-treat population, a per-protocol population, or another defined analysis set. It also does not report a missing-data method, an imputation procedure, or the number of participants with unassessed response. The endpoint definition is detailed, but the process for adjudicating response and handling assessments that did not fit the stated schedule is not reported in the registry record. Randomization and double masking are listed, but the randomization sequence, concealment process, and masking procedures are not described.

These omissions limit independent reproduction and evaluation of the sponsor’s analysis. They do not change the meaning of the recorded arm proportions, but they leave uncertainty about how the analyzed participants were selected and how the uncertainty around the sponsor’s contrast was calculated. Statistical interpretation should therefore distinguish the numerical result that the registry posts from methodological details that it does not report.

10. Confidence Intervals and Precision

The arm-specific objective response proportions are 0.79 for Arm I and 0.683 for Arm II. Their posted 95% confidence intervals are 0.729 to 0.842 and 0.615 to 0.745, respectively. These intervals express uncertainty around each arm’s response proportion; they are not the interval for the contrast between arms. The sponsor separately reports a response-rate difference of 0.107 with an 80% confidence interval from 0.052 to 0.162.

Confidence intervals help distinguish a point estimate from the range of values that remain compatible with the data and analysis. Wider intervals indicate less precision, while narrower intervals indicate greater precision, all else equal. They do not account automatically for every source of uncertainty, such as selection into the endpoint analysis or possible bias from missing assessments. The registry record does not report enough detail to assess those issues.

The sponsor’s interval has an 80% confidence level, whereas the arm-specific intervals have a 95% confidence level. These confidence levels are not interchangeable, and intervals at different confidence levels should not be compared as though they were calculated on the same basis. The record does not state why the sponsor’s contrast was reported at 80%, nor does it provide a method description that would allow the interval to be reproduced.

The posted intervals are estimates of precision for their specified quantities, not guarantees about the true response rates or a direct measure of clinical importance. The sponsor’s contrast is the relevant posted between-arm statistic for the primary response question; the separate unadjusted risk-difference calculation based on counts 2 and 1 is not the same response-rate contrast.

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 planning figures are participants per arm, not total events. The sample-size illustration uses the observed effect as its reference and considers planning for 100%, 75%, or 50% of that observed effect. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial’s own sample-size justification and design assumptions are not reported in the registry record.

For 100% of the observed effect, the illustration lists 5,355 participants per arm for 80% power and 7,169 participants per arm for 90% power. For 75% of the observed effect, it lists 10,278 participants per arm for 80% power and 13,759 participants per arm for 90% power. For 50% of the observed effect, it lists 24,829 participants per arm for 80% power and 33,239 participants per arm for 90% power.

In general, the 80% power column describes a planning scenario designed to have an 80% chance of detecting the specified effect if the assumptions are met and that effect is true. The 90% column describes a higher planned chance of detection under the same stated framework. Smaller effects are harder to distinguish from random variation, so the illustration requires more participants per arm for smaller target effects. These figures are planning illustrations based on the observed effect, not observed power, and they do not describe the number of participants actually analyzed in the trial.

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 = 0.009; treatment proportion p₁ = 0.005; average p̄ = 0.007.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1185 = 0.2323.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1185 = 0.0997.
4. n = (0.2323 + 0.0997)² / (-0.0045)² = 5,354.8, rounded up to 5,355 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 <- 0.00934579439252336                          # control proportion
p1 <- 0.00480769230769231                          # 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(98475)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 5,355 (80% power), 7,169 (90% power)
 75% of observed effect: n per arm = 10,278 (80% power), 13,759 (90% power)
 50% of observed effect: n per arm = 24,829 (80% power), 33,239 (90% power)
power.prop.test: 5354.8 
Simulated power at n = 5,355 per arm: 0.814 (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. Analyses Reported by the Sponsor

The sponsor’s own posted analysis reports a difference in response rate of 0.107, with an 80% confidence interval from 0.052 to 0.162. This is the registry’s reported analysis for the response-rate contrast. The registry does not report its method, p-value, or non-inferiority margin, so those aspects cannot be independently evaluated from the record.

A separate unadjusted calculation is also present: a risk difference of -0.004, a 95% confidence interval from -0.021 to 0.011, and p = 0.579. Its listed counts are 2 and 1, rather than the objective response proportions of 0.79 and 0.683. It should not be presented as a recalculation of the sponsor’s response-rate difference. The record does not explain what clinical outcome those counts represent.

The discrepancy flag is false, but that does not resolve the difference in the quantities represented by these results. The sponsor’s response analysis and the separate count-based calculation should be kept distinct. The reported sponsor analysis remains the relevant posted comparison for the primary endpoint, while the registry record lacks enough methodological detail to reproduce it.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists objective response during first-phase Step 1 as the primary outcome and objective response during first-phase Step 2 as a secondary outcome. It reports 2 outcome measures and 1 analysis. The primary response analysis is reported for the two Step 1 arms. The record does not provide a complete statistical analysis plan describing how multiple outcomes, time points, or comparisons were handled.

When a study examines multiple outcomes or performs multiple tests, the chance of at least one apparently unusual result can increase unless the analysis plan addresses multiplicity. This is a general statistical issue; the registry record does not say whether a multiplicity adjustment or hierarchical testing strategy was used. It also does not report whether any interim analyses were planned or conducted. The trial’s original protocol-based analysis plan is not reported in the registry record.

The endpoint population is described as eligible patients only, but the record does not define the full analysis set or state whether the primary analysis was intention-to-treat, per-protocol, or another approach. It does not report the number of missing response assessments, reasons for missingness, or how such assessments were handled. The stated schedule was assessment every 4 weeks for 16 weeks during Step 1, but the record does not explain whether all assessments were available for every analyzed participant.

Missing outcomes can affect both the estimated response proportion and the comparability of randomized groups if missingness is related to response or treatment. That is a general concern, not evidence that missing data biased this trial’s results. The registry record also does not report a sensitivity analysis examining alternative assumptions about missing responses. These absent details limit assessment of how robust the posted response estimates are to participant exclusions and incomplete outcome measurement.

15. 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: dyspnea (50.0%), hypotension (33.3%), fatigue (33.3%), dehydration (33.3%), vomiting (33.3%).

The serious adverse event figures are reported separately from the primary response analysis. For Arm I Step 1, the serious-event count is 146 among 223 at risk. For Arm II Step 1, it is 112 among 220 at risk. The registry also lists Step 2 groups with 1 among 4 and 3 among 14, and expansion groups with 2 among 4 and 1 among 3. These are counts and denominators as recorded; they should not be merged with the response-analysis arm counts.

The record lists serious adverse event terms including dyspnea at 50.0%, and hypotension, fatigue, dehydration, vomiting, and infection with grade 3-4 neutropenia, lung at 33.3% each. The registry excerpt does not give denominators or group attribution for these listed term percentages, so they should not be interpreted as rates in a particular Step 1 arm. Death counts are not reported in the registry record.

Safety counts describe the recorded events in the specified groups; they do not establish that a treatment caused an event. Small denominators in the Step 2 and expansion groups make those counts especially difficult to compare with the larger Step 1 groups. The registry record does not provide further details on event collection, attribution, or exposure time.

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

The posted response data describe objective response in the analyzed Step 1 groups: the proportion is 0.79 in Arm I and 0.683 in Arm II. The sponsor’s between-arm analysis reports a response-rate difference of 0.107 and an 80% confidence interval from 0.052 to 0.162. These results concern the registry-defined response endpoint and the analysis population used for it.

They do not establish how long responses lasted, whether there was a difference in survival, or how the regimens compare on every clinical outcome. They also do not, by themselves, describe the overall balance of benefits and harms. The registry lists serious adverse event counts, but those are reported for separate safety groups and are not a complete comparative safety analysis. No medical advice or treatment recommendation follows from these registry results.

The sponsor analysis is labelled as a non-inferiority or equivalence type, but the registry does not report a margin, method, or decision rule. The response difference and its interval should therefore be read as the reported estimate and precision, not as a reconstructed formal conclusion about non-inferiority or equivalence. The separate unadjusted calculation based on counts 2 and 1 is not the same endpoint contrast and should not be used to reinterpret the response proportions.

The trial’s randomized, double-blind, parallel-group design provides a framework for comparing assigned regimens, but key analysis details are absent. The record does not report the analysis population definition, handling of missing response assessments, or enough methodological detail to reproduce the sponsor’s result. The expansion substudy was terminated early with only 7 patients enrolled, and the registry says the clinical results presented are mainly for the first phase. Conclusions should remain limited to what the posted first-phase response data describe.

17. Why This Trial Matters Statistically

This trial illustrates why the endpoint and the analysis contrast need to be distinguished. Arm-specific response proportions describe the observed frequency of a defined event in each analyzed group; a between-arm difference summarizes their contrast. The sponsor’s response-rate difference is the relevant posted comparison for the primary endpoint, while a separate recalculation based on counts 2 and 1 does not represent that same response outcome.

It also shows why confidence intervals need to be read with their confidence level and method in view. The arm-specific response intervals are reported at 95%, while the sponsor’s difference interval is reported at 80%. The sponsor’s method and the rationale for the confidence level are not reported, and the legacy label alone does not supply a non-inferiority margin or decision rule. A numerical interval can be described accurately without overclaiming what formal conclusion it supports.

The registry’s eligibility restriction, distinct response and safety denominators, and incomplete reporting of missing-data and analysis-population procedures also matter. Randomization and masking are important design features, but they do not substitute for transparent reporting of the analysis set and outcome handling. The early-terminated expansion substudy further limits what can be learned from those groups. Together, these issues demonstrate the value of separating observed results, inferential uncertainty, and details that the registry record does not report.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The posted primary response results concern eligible patients in the first-phase Step 1 arms. The registry record does not provide a participant flow, a clear definition of the primary analysis set, or an explanation of how the response analysis counts relate to overall enrollment. Safety denominators differ from the response arm counts, and the record does not explain those differences. The results should not be treated as if every reported group shares an identical population.

The sponsor’s method, p-value, and non-inferiority or equivalence margin are not reported, despite the legacy analysis label. The sponsor’s response-rate contrast has an 80% confidence interval, while the arm proportions have 95% intervals. The record does not explain the choice of confidence level or provide enough information to reproduce the sponsor’s interval. It also does not report the trial’s original sample-size justification.

Information on missing response assessments, analysis-population rules, interim analyses, and multiplicity handling is not reported in the registry record. The expansion substudy was terminated early with only 7 patients enrolled, and clinical results are described as mainly from the first phase. The separate unadjusted comparison uses counts 2 and 1, not the posted response proportions, and the clinical meaning of those counts is not explained. These limitations constrain interpretation without changing the values the registry reports.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Lenalidomide and Dexamethasone With or Without Thalidomide in Treating Patients With Multiple Myeloma — NCT00098475.
• Registry record last updated 2026-08-28; status last verified 2026-04.
• Results first posted 2014-01-22.
• 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

NCT00098475 is a randomized, double-blind, parallel-group phase III trial sponsored by the National Cancer Institute. It studies lenalidomide with standard-dose dexamethasone versus lenalidomide with low-dose dexamethasone for multiple myeloma, with thalidomide and dexamethasone salvage treatment described for non-responders. The primary endpoint is the proportion with objective response during first-phase Step 1.

The posted response proportions are 0.79 for Arm I and 0.683 for Arm II. The sponsor reports a response-rate difference of 0.107 with an 80% confidence interval from 0.052 to 0.162. The registry notes that the expansion substudy ended early with only 7 patients enrolled and that the clinical results are mainly from the first phase. Important details, including the sponsor’s analysis method, missing-data handling, and original sample-size justification, are not reported in the registry record.