A Study of Lenalidomide Versus Placebo in Subjects With Transfusion Dependent Anemia in Lower Risk Myelodysplastic Syndrome (MDS) Without Del 5q: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Lenalidomide Versus Placebo in Subjects With Transfusion Dependent Anemia in Lower Risk Myelodysplastic Syndrome (MDS) Without Del 5q (NCT01029262), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Achieved Red Blood Cell (RBC) Transfusion Independence for ≥ 56 Days as Determined by an Independent Review Committee (IRC).

2. Clinical Question

The clinical question is specific to transfusion-dependent anemia in the recorded MDS risk groups and without deletion 5q. It is not a comparison across all people with anemia or all MDS categories. The registry lists 239 participants enrolled. The results should be read within the trial’s stated population, outcome definition, and follow-up conditions rather than generalized beyond them.

3. Trial Design

The registry describes a randomized, Phase 3, parallel-group study comparing lenalidomide with placebo. Its title characterizes the study as multicenter and double-blind, while the registry’s masking field lists quadruple masking; no explanation of that wording difference is reported in the registry record. The status is completed, and enrollment is listed as 239.

Participants were assigned to lenalidomide or placebo. The intent-to-treat population for the primary endpoint included all randomized participants. The posted endpoint groups contain 160 participants in the lenalidomide arm and 79 in the placebo arm. The primary outcome was assessed from the first study-drug dose until 28 days after the last dose, as of the data cut-off date of 17 March 2014. The registry reports median treatment durations of 168 days and 164 days for the two groups, respectively, with minimum and maximum durations also recorded.

The lenalidomide arm description includes oral daily dosing and refers to 10 mg for participants with creatinine clearance ≥ 60 mL/min. Its text is cut off before the full description of dosing for participants outside that criterion, so the complete regimen is not reported in the registry record. The placebo arm is described as three placebo capsules once daily for at least 168 days, subject to disease progression, intolerable side effects, or withdrawal of consent. The study summary says that the trial investigated both red blood cell transfusion needs and safety.

The registry lists outcomes spanning transfusion independence, erythroid response, progression to acute myeloid leukemia, overall survival, adverse events, and quality of life. The original sample-size justification, the detailed statistical analysis plan, and any interim-analysis plan are not reported in the registry record. The posted design details therefore support interpretation of the recorded comparison, but do not establish how the study’s original design decisions were made.

4. Participant Flow and Accounting

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

Before assignment: Participants must have had transfusion-dependent anemia defined as having an average transfusion need of at least 2 units of packed red blood cells (pRBCs) per 28 days during the 112 days preceding randomization; No consecutive 56-day period that was RBC-transfusion-free during the 112 days preceding randomization; hemoglobin levels ≤ 9.5 g/dL.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent-to-Treat (ITT) population includes all participants who were randomized to either lenalidomide or placebo.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The Intent-to-Treat (ITT) population includes all participants who were randomized.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Achieved Red Blood Cell (RBC) Transfusion Independence for ≥ 56 Days as Determined by an Independent Review Committee (IRC), measured over From first dose of study drug until 28 days after the last dose, as of the data cut-off date of 17 March 2014; median (minimum, maximum) duration of treatment was 168 (14, 449) and 164 (7, 1158) days in each treatment group respectively..

The primary endpoint was the percentage of participants who achieved red blood cell transfusion independence for at least 56 days, determined by an independent review committee. A participant qualified by having no red blood cell transfusions during any consecutive rolling 56-day interval within the double-blind treatment phase. The record defines that phase as starting with the first dose and continuing until 28 days after the last study-drug dose, and gives examples of consecutive intervals beginning on different study days.

This endpoint turns a pattern of transfusion use into a binary response: a participant either met the specified criterion or did not. It is used to address whether participants experienced a qualifying period without transfusions, rather than to measure a continuous change in transfusion frequency or the total duration of independence. A qualifying response does not by itself describe symptoms, quality of life, survival, or the overall course of MDS.

The endpoint is tied to a defined observation window and a specific decision rule. The rolling-window definition allows a qualifying period to begin at different points during treatment, while the requirement for a full 56-day interval sets a minimum duration for response classification. The intent-to-treat population includes everyone randomized, as defined in the record. That population definition matters because it anchors the reported percentages to treatment assignment, rather than only to participants who completed treatment or had a particular post-randomization experience.

The endpoint is a measure of response occurrence, not proof of a mechanism or of a lasting benefit after treatment. The registry’s secondary outcomes include a longer transfusion-independence duration and time to response, which address different aspects of response than the primary binary endpoint.

7. Results Posted in the Registry

• Lenalidomide: 26.9% (43/160) versus 2.5% (2/79) on control; risk difference 24.3 percentage points (95% CI 16.7 to 32.0), risk ratio 10.62 (2.64–42.70); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Participants Who Achieved RBC Transfusion Independence With a Duration of ≥ 24 Weeks (168 Days) as Determined by the Sponsor

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Lenalidomide: 17.5% (28/160) versus 0.0% (0/79) on control; risk difference 17.5 percentage points (95% CI 11.6 to 23.4); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Lenalidomide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Achieved an Erythroid Response Based on the Modified International Working Group (IWG) 2006 Criteria

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Lenalidomide: 38.8% (62/160) versus 30.4% (24/79) on control; risk difference 8.4 percentage points (95% CI -4.3 to 21.0), risk ratio 1.28 (0.87–1.88); unadjusted two-proportion z-test p = 0.205.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lenalidomide and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the scope beyond the primary 56-day response. They include a longer-duration transfusion-independence measure, erythroid response, time to response, AML progression, overall survival, adverse events, and quality-of-life compliance. These outcomes concern different aspects of efficacy, safety, and follow-up, so they do not all serve as direct replications of the primary endpoint.

The posted results indicate that the longer-duration transfusion-independence outcome was recorded more often in the lenalidomide group, while the erythroid-response percentages were also numerically higher in that group. The sponsor’s analysis for erythroid response, however, does not provide the same statistical signal as the primary endpoint. This variation is not inherently inconsistent: response definitions differ, and the qualifying criteria for a longer response or an erythroid response are not identical to the primary rolling 56-day endpoint.

The registry lists many secondary outcomes, but the presence of an outcome in the registry does not mean every result is fully reported in the available record. Numerical results for AML progression, overall survival, time to response, and quality-of-life compliance are not included in the summarized outcomes described in this record. Their absence from these posted summaries should not be interpreted as a null finding; the relevant result is not reported in the registry record.

Unadjusted secondary tests carry less confirmatory weight when many outcomes are examined. With multiple comparisons, the chance of seeing some apparently notable results can increase. The registry does not report whether a multiplicity adjustment, a prespecified testing hierarchy, or another method was used. Secondary outcomes can add context and generate hypotheses, but should not be counted as independent proof of the primary result or used to infer an unreported finding.

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

• Percentage of Participants Who Achieved RBC Transfusion Independence With a Duration of ≥ 24 Weeks (168 Days) as Determined by the Sponsor
• Kaplan Meier Estimates of Duration of 56-day RBC Transfusion Independence Response as Determined by the Sponsor
• Percentage of Participants Who Achieved an Erythroid Response Based on the Modified International Working Group (IWG) 2006 Criteria
• Time to 56-Day RBC-Transfusion-Independent (TI) Response as Determined by the Sponsor
• Kaplan Meier Estimates for Progression to Acute Myeloid Leukemia (AML)
• Kaplan Meier Estimate for Overall Survival (OS)
• Number of Participants With Treatment Emergent Adverse Events (TEAE)
• Compliance Rates Using the European Organization for Research and Treatment of Cancer Quality of Life Questionnaire (EORTC QLQ-C30) From Baseline to Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary endpoint is binary: each participant is classified according to whether they achieved the specified 56-day transfusion-independent response. The arm percentages describe the proportion meeting that criterion in each randomized group. A risk ratio compares those proportions by expressing one group’s response rate relative to the other group’s rate. It is not an absolute percentage-point difference, and its value depends on the response rates in both groups.

The posted recalculation is an unadjusted comparison of the group summaries. It does not account for covariates or other features of individual participant data. The record reports the sponsor’s own analysis using Fisher’s exact method and a risk ratio. Because the discrepancy flag is false, no conflict between the posted recalculation and the sponsor’s reported result is identified. The sponsor’s analysis remains the trial’s reported analysis.

Why use Fisher’s exact method?

Fisher’s exact test is a method for comparing categorical outcomes between groups. It evaluates how compatible the observed allocation of responders and nonresponders is with a null hypothesis of no association between group and response, under the test’s assumptions. Unlike an approximation that relies on large-sample behavior, the exact method calculates probabilities based on the possible arrangements of the observed counts. It is commonly useful when response counts are sparse, as they are in the placebo group for this endpoint.

A p-value summarizes how unusual data at least as inconsistent with the null hypothesis would be if the null model were true. It is not the probability that the null hypothesis is true, nor the probability that the result occurred by chance in an ordinary-language sense. Statistical significance does not measure effect size, establish clinical importance, or show that all relevant biases have been eliminated.

What does the confidence interval describe?

A confidence interval gives a range of estimates compatible with the data under the method used, while reflecting sampling uncertainty. For the sponsor’s risk ratio, the interval is 2.639 to 42.702 at the 95% confidence level. It lies above the no-difference value of 1, consistent with the reported test result, but it is wide. This means that the data are less precise about the magnitude of the relative effect than the small p-value alone might suggest. The interval does not capture every possible source of uncertainty, such as limitations in the recorded analysis or applicability to other populations.

Why distinguish the primary and secondary outcomes?

The primary endpoint is the trial’s designated main outcome in the registry record. Secondary endpoints examine other clinical or safety dimensions, including longer-duration response, erythroid response, time to response, survival-related outcomes, adverse events, and quality of life. Different endpoint definitions can yield different patterns without being contradictory. For example, meeting a 56-day response criterion is not the same as sustaining independence for a longer duration, and neither is equivalent to an erythroid response classification.

When many outcomes are examined, some nominally small p-values may arise even when there is no underlying effect for some outcomes. Adjustments or a prespecified hierarchy can address aspects of this multiplicity, but the approach used for this trial is not reported in the registry record. Consequently, unadjusted secondary comparisons should be viewed as supportive or exploratory rather than treated as a collection of separate confirmatory findings.

What do the recalculations and planning illustrations mean?

A recalculated comparison uses posted group-level summary statistics to perform a simple unadjusted calculation. It is not a replacement for the sponsor’s analysis, which is the analysis reported by the trial. The primary risk-ratio result in the sponsor analysis and the posted recalculation have p-values below 0.001, and the record marks no discrepancy. For the erythroid-response outcome, the sponsor’s reported p-value is 0.252, while the unadjusted recalculation gives 0.205. Those are not identical analyses, and they do not support treating the recalculation as an exact reproduction of the sponsor’s method.

Planning illustrations use the observed effect as a reference to show how a future study’s required arm size changes under stated assumptions. They do not reconstruct the original trial’s design process. Their assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect expressed as a stated fraction of the observed effect. The original trial’s sample-size assumptions are not reported in the registry record.

For binary outcomes, an observed percentage is a group-level summary; the individual response classification is still binary. More generally, statistical methods must match the outcome type and its distribution. For count outcomes, over-dispersion can matter when variability exceeds what a simple model assumes, and failing to allow for it can make uncertainty appear too small. That is a general statistical point, not a description of the analysis used for this trial. The primary endpoint is not a count outcome, and no over-dispersion model for it is reported.

The registry specifies the intent-to-treat population for the primary endpoint as all randomized participants. That is an important analysis-population definition, but it does not tell readers how every missing or unevaluable outcome was handled. The missing-data procedure and sensitivity analyses are not reported in the registry record. Likewise, the existence of a reported analysis does not establish whether all outcome definitions and analysis choices were fixed before unblinding; that information is not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s reported risk ratio for the primary endpoint is 10.616, with a 95% confidence interval from 2.639 to 42.702. The interval excludes 1, the value corresponding to equal response rates in a ratio comparison. This is consistent with the reported p-value of p < 0.001. However, the interval spans a broad range of relative effects, so the estimate is more informative about the direction of the observed comparison than about its precise magnitude.

The interval’s width reflects sampling uncertainty in the estimated ratio. In general, confidence intervals are useful because they show a range of values compatible with the data and analysis, rather than offering only a point estimate. They do not mean that there is a 95% probability that the true effect lies in this particular interval. Nor do they account for every uncertainty, including potential limitations in measurement, missing-data handling, analysis choices, or generalizability.

The low placebo response percentage is relevant to interpretation of the relative measure: when one group’s rate is low, a ratio can be large even when the absolute difference is more modest. The arm percentages are 2.5% for placebo and 26.9% for lenalidomide. These percentages and the risk ratio communicate different aspects of the result, and should not be conflated.

The posted recalculation gives a risk-difference interval in more precise decimal form, but the registry’s sponsor analysis is the trial’s own reported result. The record does not report a sponsor confidence interval for the absolute percentage-point difference. Precision about the relative comparison should therefore not be mistaken for equally precise knowledge of every effect scale or every clinical consequence.

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 sample-size illustrations show participants per arm for the binary outcomes. They are not total event counts. Their purpose is to illustrate how a future study’s planned arm size would change under the stated assumptions and chosen effect size. For the primary endpoint, the rows correspond to planning for 100%, 75%, and 50% of the observed effect. The required participant count increases as the effect being targeted becomes smaller.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The columns labeled for 80% and 90% power indicate the number of participants per arm required, under those assumptions, to have the corresponding chance of detecting an effect of the specified size if that effect is real. Higher planned power generally requires more participants for the same target effect.

These are planning illustrations based on the observed result, not the original design calculation. The original trial’s sample-size justification and assumptions are not reported in the registry record. The displayed counts should not be read as a statement about what the trial actually planned or as evidence that the trial had a particular power after its results were known. This is not observed power.

Because the observed effect can itself be uncertain, using it as a planning reference does not guarantee that a future study will have the same underlying effect. The illustrations also depend on the specified test and assumptions, so they are not universal sample-size recommendations. The useful reading is comparative: smaller target effects require more participants, and the higher power target requires a larger planned sample for a given effect.

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 = 0.025; treatment proportion p₁ = 0.269; average p̄ = 0.147.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5008 = 0.9816.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4703 = 0.3958.
4. n = (0.9816 + 0.3958)² / (0.2434)² = 32.0, rounded up to 33 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 <- 0.0253164556962025                          # control proportion
p1 <- 0.26875                          # 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(1029262)
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 = 33 (80% power), 43 (90% power)
 75% of observed effect: n per arm = 48 (80% power), 63 (90% power)
 50% of observed effect: n per arm = 83 (80% power), 110 (90% power)
power.prop.test: 32 
Simulated power at n = 33 per arm: 0.887 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Fisher exact comparison of the risk ratio. The reported estimate is 10.616, with a 95% confidence interval from 2.639 to 42.702 and p < 0.001. The posted simple recalculation also gives p < 0.001, and the record marks no discrepancy. The sponsor’s reported analysis is therefore the trial’s own inferential result; the recalculation is a supplementary unadjusted analysis of posted summaries.

These analyses may use different computational details or conventions, so they should not be treated as interchangeable simply because they address the same group comparison. Where a discrepancy is flagged, the sponsor’s own analysis takes precedence. No such discrepancy is flagged for the primary endpoint in this record.

For the erythroid-response secondary outcome, the sponsor reports a risk ratio of 1.276 with a 95% confidence interval from 0.867 to 1.877 and p = 0.252. The simple unadjusted recalculation gives p = 0.205. This difference illustrates that a recalculation from posted summaries need not reproduce the sponsor’s inferential result exactly. The sponsor analysis remains the appropriate reference for what the trial reported, while the recalculation is best understood as a separate, limited check rather than a correction.

For the longer-duration transfusion-independence outcome, the registry reports a sponsor p-value of p < 0.001. The record’s reporting for that analysis does not give a complete finite confidence interval for the risk ratio. The posted values should therefore be read with attention to what is and is not reported, rather than assuming that every sponsor analysis provides the same set of statistical details.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and lists numerous secondary outcomes, but it does not report how multiplicity was handled. It is not reported in the registry record whether secondary hypotheses were tested in a prespecified order, whether p-values were adjusted, or whether any family of outcomes was treated as confirmatory. When many statistical tests are performed, unadjusted p-values can overstate the strength of evidence if they are interpreted as though only one test had been planned. This is why secondary results generally require more cautious interpretation.

The primary endpoint’s analysis population is specified as the intent-to-treat population, including all randomized participants. That definition does not fully describe the handling of missing endpoint measurements. The missing-data method, the number of participants with missing primary outcomes, and any sensitivity analyses for missingness are not reported in the registry record. It is therefore not possible to determine from the record whether missing outcomes were treated as nonresponses, excluded, imputed, or handled by another procedure.

The record does not report whether interim analyses were conducted or whether they could have affected the statistical threshold or conduct of the study. The original sample-size justification and the trial’s full statistical analysis plan are also not reported in the registry record. These absences limit assessment of whether the posted analysis exactly reflects prespecified procedures, but they do not by themselves establish that procedures were inappropriate.

Randomization and the intent-to-treat definition provide important structure for the primary comparison, but they do not answer every question about adherence, follow-up, outcome ascertainment, or analysis decisions. The registry says the primary response was determined by an independent review committee, which is relevant to outcome assessment. Details beyond the stated endpoint definition and reported method are not reported in the registry record. These uncertainties should be kept distinct from the statistical result itself: they qualify how fully the result can be audited from the registry record, rather than changing the reported numbers.

16. 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: pneumonia (6.2%), anaemia (3.1%), atrial fibrillation (2.5%), cardiac failure (2.5%), bronchitis (2.5%).

The registry’s adverse-event summary lists serious adverse events affecting 16 of 79 participants in the placebo group and 62 of 160 participants in the lenalidomide group. It also lists other adverse events affecting 70 of 79 and 154 of 160 participants, respectively. These are group-specific counts and denominators; they should not be added together, because the record does not establish that the categories are mutually exclusive.

The record lists deaths as 43 in the placebo group and 94 in the lenalidomide group. These counts alone do not describe cause, timing, attribution, or a comparison adjusted for duration of follow-up. The median treatment durations and observed ranges differed between groups, and the available figures do not provide enough detail to infer why deaths occurred or whether they were caused by study treatment.

Among the listed serious adverse-event terms, pneumonia is reported at 6.2%, anemia at 3.1%, and atrial fibrillation, cardiac failure, bronchitis, and acute myeloid leukemia at 2.5% each. The record’s summary does not establish that these events were caused by the assigned treatment. Adverse-event counts are descriptive safety information; interpreting comparative risk requires attention to event definitions, follow-up, exposure, and attribution, details that are not fully reported in the registry record.

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

The primary result shows that a larger percentage of participants assigned to lenalidomide achieved the trial-defined red blood cell transfusion-independence response for at least 56 days than participants assigned to placebo. The sponsor’s risk-ratio analysis reports a statistically significant group comparison, with a confidence interval that excludes 1. This is evidence about the specified endpoint in the trial population and under the recorded analysis.

The result does not mean that every participant assigned to lenalidomide achieved transfusion independence. The reported group percentage was 26.9%, and the response definition concerned at least one qualifying rolling 56-day interval during the specified treatment phase. It does not establish that a response continued after the interval, after treatment, or indefinitely. Nor does it by itself describe the number or timing of transfusions outside a qualifying interval.

The primary endpoint does not directly establish effects on survival, AML progression, quality of life, or all forms of anemia. Those questions require their own outcome data and analyses. Although the registry lists those outcomes, results for some are not reported in the registry record represented by the posted summaries. The adverse-event counts also cannot, on their own, determine treatment causality or balance benefits and harms.

Statistical significance is not the same as clinical importance. The wide confidence interval means the relative effect’s magnitude remains imprecisely estimated, even though the result is inconsistent with a risk ratio of 1 under the reported analysis. The study’s eligibility description also limits direct generalization: the findings concern transfusion-dependent anemia in low or intermediate-1 risk MDS without deletion 5q, in participants described as unresponsive or refractory to erythropoiesis-stimulating agents. They do not settle outcomes in other populations, treatment settings, or conditions.

18. Why This Trial Matters Statistically

This trial illustrates how a clearly defined binary endpoint can make a clinical question statistically tractable. Transfusion independence was not treated as a vague impression: the registry defined a qualifying response as a rolling interval of 56 days without red blood cell transfusion. That rule makes the outcome more reproducible and allows the groups to be compared using a specified response proportion.

The primary comparison also demonstrates why effect measures and precision should be read together. A risk ratio can communicate a strong relative contrast when the placebo response rate is low, while its confidence interval can remain wide. The p-value addresses compatibility with a null comparison under the method; it does not quantify the size, practical importance, or certainty of every aspect of the effect. Reading the group percentages, ratio, interval, and endpoint definition together gives a more complete statistical interpretation.

The record offers a further lesson in separating the primary result from a broad set of secondary outcomes. Longer response duration, erythroid response, time to response, survival, safety, and quality of life are related but distinct questions. Their evidence does not become equally strong simply because each appears in the same trial record. Without reported information on multiplicity, secondary tests deserve particular caution.

Finally, trial interpretation depends on transparent reporting of the analysis population, missing-data handling, prespecified methods, and safety follow-up. The record gives the primary intent-to-treat definition and sponsor analysis, but does not report several details needed for a full audit of analysis decisions. This makes the trial useful for teaching both how randomized comparisons inform an endpoint-specific question and why a statistically significant result should still be read within the limits of its reporting.

19. 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 does not include the original sample-size justification or the assumptions used to design the trial. The sample-size illustrations based on the observed effect are not evidence of the trial’s planned power. The statistical analysis plan, interim-analysis procedures, and approach to multiplicity are also not reported in the registry record, limiting assessment of whether all reported analyses followed prespecified choices.

Although the primary population is defined as all randomized participants, the record does not report the number of missing primary outcomes or how missingness was handled. It does not give sensitivity analyses for alternative missing-data assumptions. The sponsor’s primary analysis is reported, but the record does not provide enough detail to reconstruct every aspect of the analysis from individual participant data.

The confidence interval for the sponsor’s primary risk ratio is wide, so the relative effect’s magnitude is uncertain. The primary outcome is a binary response based on a qualifying interval and does not measure sustained independence beyond that definition. The secondary endpoints differ in definition, and outcomes listed without posted numerical results cannot be used to draw conclusions from their registry listing alone.

Generalizability is restricted by the recorded population: transfusion-dependent anemia associated with low or intermediate-1 risk MDS without deletion 5q, and described as unresponsive or refractory to erythropoiesis-stimulating agents. The arm description for lenalidomide is truncated, so the complete dosing details are not reported in the registry record. Masking is described as quadruple in the registry field and double-blind in the study title, with no explanation of that difference. Safety summaries provide counts and selected event terms, but do not fully describe timing, attribution, or exposure-adjusted comparisons. These limitations constrain interpretation without negating the reported primary comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Lenalidomide Versus Placebo in Subjects With Transfusion Dependent Anemia in Lower Risk Myelodysplastic Syndrome (MDS) Without Del 5q — NCT01029262.
• Registry record last updated 2019-06-25; status last verified 2019-06.
• Results first posted 2015-06-18.
• 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.

23. Record Summary

This completed randomized Phase 3 parallel-group trial compared lenalidomide with placebo in participants with transfusion-dependent anemia due to low or intermediate-1 risk MDS without deletion 5q. The registry lists 239 participants enrolled and defines the primary population as all randomized participants.

The primary endpoint was red blood cell transfusion independence for at least 56 days, determined by an independent review committee. The recorded response percentages were 26.9% with lenalidomide and 2.5% with placebo. The sponsor reported a risk ratio of 10.616, a 95% confidence interval from 2.639 to 42.702, and p < 0.001.

Secondary outcomes and safety summaries provide additional context, but their interpretation depends on outcome definitions, multiplicity, missing-data handling, and follow-up. Several analysis details are not reported in the registry record. The findings therefore speak most directly to the specified primary endpoint and trial population.