Pomalidomide in Combination With High Dose Dexamethasone and Oral Cyclophosphamide: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pomalidomide in Combination With High Dose Dexamethasone and Oral Cyclophosphamide (NCT01432600), a randomized phase 1, phase 2 study. The primary outcome is Phase II - Overall Response Rate (ORR).

2. Clinical Question

The central statistical contrast is between the two Phase II regimens. The registry reports an overall response rate of 38.9% for pomalidomide and dexamethasone, with a 95% confidence interval from 23.0% to 54.8%. For the arm that also included cyclophosphamide, the reported rate is 64.7%, with a 95% confidence interval from 48.6% to 80.8%. These are estimates of the proportions meeting the registry’s response definition in the respective arms; they are not direct measures of the duration of response or of survival.

The registry identifies the study as randomized, but also labels its model as single group. It describes randomized Phase II arms and a crossover pathway, so the record contains more than one design description. The detailed allocation method and the analysis population used for the arm comparison are not reported in the registry record. That limits how completely the comparison can be reconstructed from the record alone.

3. Trial Design

The registry describes a Phase I and Phase II study of pomalidomide with high-dose dexamethasone, with oral cyclophosphamide included in some regimens. The study is marked completed, with planned enrollment of 80. The registry lists randomized allocation and no masking, while its model field says single group. Those entries do not fully align with the arm descriptions, which include randomized Phase II regimens. The detailed method used to generate or conceal allocation is not reported in the registry record.

In Phase I, the record describes dose escalation of cyclophosphamide in combination with pomalidomide and dexamethasone. The primary endpoint, however, is explicitly a Phase II outcome: overall response rate in all Phase II participants. Its reported arm estimates are for pomalidomide plus dexamethasone and for pomalidomide plus dexamethasone plus cyclophosphamide. The registry also lists a crossover arm. Participants in the pomalidomide-and-dexamethasone arm who experienced progressive disease were allowed to cross over at the treating physician’s discretion, with cyclophosphamide added.

The reported Phase II arm sizes are 36 for pomalidomide and dexamethasone and 34 for the combination including cyclophosphamide. The registry separately reports 80 as enrollment; the relationship between this enrollment figure and the participants in the outcome arms is not explained in the registry record. The record names progression-free survival, overall survival, and possibly related adverse events as secondary outcomes, but detailed results for those outcomes are not included in the listed summary. The schedule and rules for follow-up, analysis timing, and handling of crossovers 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All Phase I Participants.

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: All participants. Arm D (a part of Arm B) started in July 2012 when, per protocol guidelines, 17 participants from Arm B elected to crossover to Arm D. Some measures may include arm D, making the total of participants evaluated higher.

6. Primary Endpoint

The registry lists the primary outcome as Phase II - Overall Response Rate (ORR), measured over 36 Months.

The primary endpoint is Phase II overall response rate, expressed as the percentage of participants with an overall response of minimal remission or better. The registry specifies the International Myeloma Working Group uniform response criteria and notes that minimal response was incorporated for participants with relapsed or refractory myeloma. It defines minimal response using reductions in serum paraprotein and urine light-chain excretion, with a reduction in the size of soft-tissue plasmacytoma required when applicable. The listed timeframe is 36 Months.

A response-rate endpoint is a binary outcome at the participant level: a participant either meets the response definition or does not. The rate summarizes the proportion meeting that definition within an arm. In general, such endpoints can provide a clear measure of whether participants reached a prespecified response threshold, but they do not describe how long a response lasted. Nor does an overall response rate alone describe progression-free or overall survival, both of which the registry lists separately as secondary outcomes.

The endpoint is reported by treatment arm, making the rates relevant to the stated Phase II comparison. The registry does not report additional detail about response assessment procedures, review independence, or how missing or unevaluable assessments were handled. Those omissions matter because the endpoint depends on applying response criteria to participant-level assessments.

7. Results Posted in the Registry

• C: Pomalidomide, Dexamethasone, Cyclophosphamide: 64.7% (22/34) versus 38.9% (14/36) on control; risk difference 25.8 percentage points (95% CI 3.2 to 48.4), risk ratio 1.66 (1.03–2.69); unadjusted two-proportion z-test p = 0.031.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either meets the overall-response definition or does not. The arm-level percentage is the proportion meeting that definition. In general, an estimate based on a limited group of participants varies from sample to sample, even when the underlying response probability is unchanged. Confidence intervals express that sampling uncertainty; they are not guarantees that a particular interval contains the true value.

What do the confidence intervals describe?

The registry reports a 95% confidence interval for each arm’s response rate. In general, a confidence interval is constructed using a method that, under its assumptions and repeated use, would cover the quantity being estimated at the stated rate. For a reader, the interval gives a range of values compatible with the observed data and method. It should not be read as a range containing most individual participant outcomes, nor as a probability statement about the fixed underlying rate after the data have been observed.

The two intervals are uncertainty ranges for separate arm rates. Their overlap or separation is not, by itself, a formal test of the difference between arms. A direct comparison uses a statistic designed for the contrast. The registry reports a risk-difference comparison and an unadjusted p-value, but does not report full details of the statistical procedure or whether covariates were included. No adjusted analysis is listed.

How should the p-value be read?

In general, a p-value is calculated under a null hypothesis, often representing no difference between arms. It describes how unusual data at least as incompatible with that null model would be, assuming the model and analysis assumptions hold. It does not measure the probability that the result is false, and it does not measure the size or importance of an effect. The registry reports p = 0.031 without an adjustment. The analysis plan, including any prespecified threshold or multiplicity strategy, is not reported in the registry record.

The record contains both arm-specific response summaries and a comparison, but it does not provide participant-level data or a detailed methods account. The comparison should therefore be understood through the quantities actually reported rather than by attempting to reconstruct an unreported model. The registry record identifies a randomized Phase II comparison, yet the model field says single group. The available design descriptions do not resolve this discrepancy in terminology.

Why do allocation and crossover matter?

In general, random allocation can make groups more comparable at the start of a trial, reducing systematic differences in measured and unmeasured factors on average. That benefit depends on the allocation being implemented as intended and on an analysis that respects the randomized comparison. The registry marks allocation as randomized, but the sequence-generation and allocation-concealment methods are not reported in the registry record. The record also says masking was none.

Crossover means some participants may receive a different regimen after an event or decision. In this study, participants in the pomalidomide-and-dexamethasone arm who experienced progressive disease could cross over at the treating physician’s discretion, with cyclophosphamide added. In general, crossover can make later outcomes harder to attribute to the initially assigned regimen. How crossover was addressed analytically is not reported in the registry record. The registry’s primary endpoint is an arm-specific response rate, and the record does not explain whether response after crossover was included or how such cases were classified.

What is the role of over-dispersion?

For a simple binary outcome, standard methods often assume that participants’ outcomes are independent and that the probability of an event is adequately represented by the model. In general, over-dispersion refers to greater variability than a model expects. If participants’ outcomes are more alike within clusters, or the model otherwise understates variability, standard errors can be too small and confidence intervals too narrow. The registry does not report a clustered analysis or evidence of over-dispersion, so it is not possible to determine whether this issue arose. It should not be assumed either way.

The response criteria also involve clinical assessments, including laboratory measures and, when applicable, soft-tissue plasmacytoma size. In general, differences in assessment timing, completeness, or interpretation can affect a binary classification. The registry specifies the criteria but does not report independent review procedures, adjudication, or missing-assessment rules. Those details would help evaluate the reliability and reproducibility of the endpoint.

What analyses are absent?

The record lists three secondary outcomes: median progression-free survival, median overall survival, and occurrence of possibly related adverse events. It reports five outcome measures in total but no analyses in its analysis count. Detailed results, analysis populations, adjustment methods, and handling of censoring or missing outcomes are not reported in the registry record. The absence of these details does not establish that analyses were not conducted; it means the record does not describe them. The posted primary result is therefore best interpreted as a limited arm-level summary rather than a complete account of the statistical analysis.

10. Confidence Intervals and Precision

The 95% confidence interval for the response rate with pomalidomide and dexamethasone extends from 23.0% to 54.8%. For the arm including cyclophosphamide, it extends from 48.6% to 80.8%. Both intervals are broad, indicating that the arm-specific rates are estimated with appreciable uncertainty. The point estimate in each arm is only one value within its interval; the full interval conveys more about precision than the point estimate alone.

In general, interval width depends on factors including the amount of information in the data, the outcome’s variability, and the method used. Wider intervals leave more uncertainty about the underlying arm rate. They do not imply that the observed rates are incorrect, and narrower intervals would not by themselves address possible bias, missing data, or limitations of the design.

The registry also reports a confidence interval for the between-arm risk difference in fractional form, but those figures have more than three decimal places. For consistency with the stated number-format limit, they are not repeated. The arm-specific intervals should not be treated as a replacement for the interval on the between-arm contrast: they answer a different question. The comparison’s unadjusted p-value is reported, but the precision of the contrast is most directly conveyed by its own interval and the assumptions behind its calculation.

The registry does not report enough methodological detail to assess the confidence-interval construction fully, including the treatment of missing assessments. The intervals describe statistical precision conditional on the data and method; they do not capture every source of uncertainty about study conduct, endpoint classification, or applicability beyond the enrolled participants.

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. They are illustrative calculations based on the observed effect, not the original trial’s documented design assumptions. The original sample-size justification is not reported in the registry record. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted is the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the planning calculation indicates would be needed to have an 80% chance of detecting the target effect under those assumptions. The 90% power column gives the corresponding planning number for a 90% chance. These are design probabilities under the assumed model and effect size; they are not probabilities that the result is true. This is not observed power.

Planning for 100% of the observed effect gives 58 participants per arm for 80% power and 77 participants per arm for 90% power. For 75% of the observed effect, the figures are 104 and 138 participants per arm. For 50% of the observed effect, they are 233 and 311 participants per arm. The pattern illustrates a general principle: smaller effects require more participants to detect with the same target power, all else equal.

These calculations should not be mistaken for the study’s enrollment targets or for a reconstruction of its protocol. They rely on a post hoc observed effect as the planning reference, and the registry does not report the trial’s original sample-size assumptions. The curve is a visual expression of how the required planning size changes with the effect used; it does not change the assumptions or turn the illustration into evidence about the trial’s achieved power.

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 = 0.389; treatment proportion p₁ = 0.647; average p̄ = 0.518.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7066 = 1.3850.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6827 = 0.5745.
4. n = (1.3850 + 0.5745)² / (0.2582)² = 57.6, rounded up to 58 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 <- 0.388888888888889                          # control proportion
p1 <- 0.647058823529412                          # 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(1432600)
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 = 58 (80% power), 77 (90% power)
 75% of observed effect: n per arm = 104 (80% power), 138 (90% power)
 50% of observed effect: n per arm = 233 (80% power), 311 (90% power)
power.prop.test: 57.6 
Simulated power at n = 58 per arm: 0.805 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary response-rate endpoint and three secondary outcomes: median progression-free survival, median overall survival, and occurrence of possibly related adverse events. It also reports five outcome measures in total. The statistical plan for prioritizing these outcomes or controlling the risk of false-positive findings across multiple comparisons is not reported in the registry record.

Multiplicity arises when researchers evaluate several outcomes, comparisons, subgroups, or time points. In general, the more analyses considered, the greater the chance that at least one apparently notable result may occur by chance if each is judged separately. Adjustments or prespecified hierarchies can address this concern, but the record does not say whether either was used. The reported p-value is unadjusted, so it should not be interpreted as accounting for other endpoints or comparisons.

The registry does not report an analysis population definition beyond describing the primary endpoint population as all Phase II participants. It does not specify whether the arm-level analysis followed intention-to-treat principles, whether participants were analyzed as assigned, or how protocol deviations and crossover were handled. It also does not describe missing response assessments, unevaluable participants, or imputation methods. These details are important for a response endpoint because the estimated percentage depends on which participants are included in the denominator and how absent assessments are classified.

The registry’s crossover description raises a further analysis question: participants in arm B could receive cyclophosphamide after progressive disease, at the treating physician’s discretion. The record does not explain how such treatment changes were handled for the primary response comparison or the listed survival outcomes. For time-to-event outcomes, censoring rules and follow-up completeness would also be relevant; these methods are not reported in the registry record.

These omissions do not establish that the analyses were inappropriate or that data were missing. They limit what can be concluded about analysis choices from the registry record. Without the statistical analysis plan and fuller outcome reporting, it is not possible to assess prespecification, multiplicity control, missing-data handling, or the exact population underlying every result.

14. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (30.0%), sepsis (20.0%), lung infection (17.6%), general disorders - other (11.8%), infections and infestations - other (11.8%).

The registry reports participants affected by serious adverse events in each listed group: 10 in the Phase I dose-escalation arm, 11 in the pomalidomide-and-dexamethasone arm, 19 in the arm including cyclophosphamide, and 9 in the crossover arm. The corresponding numbers at risk are 10, 36, 34, and 17. These are group-specific counts. The record does not report death counts.

For other adverse events, the registry reports 10 affected in the dose-escalation arm, 35 in the pomalidomide-and-dexamethasone arm, 33 in the arm including cyclophosphamide, and 15 in the crossover arm. These counts are not interchangeable with serious-event counts: they refer to a separate adverse-event category in the registry. The record lists febrile neutropenia, sepsis, and lung infection among the leading serious-event terms, with reported percentages of 30.0%, 20.0%, and 17.6%, respectively. The denominator for those term percentages is not reported in the registry record.

In general, adverse-event counts describe events or participants under the registry’s reporting definitions; they do not by themselves establish causation. Comparisons across these groups also require caution because the arms have different sizes and include different study phases or crossover status. The registry does not provide enough detail to determine exposure duration, event onset, grading rules, or the full relationship of each event to treatment.

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

The result is an arm-level comparison of overall response rates under the registry’s stated response definition. The reported rate is 38.9% for pomalidomide with dexamethasone and 64.7% for the regimen that also includes cyclophosphamide. The confidence intervals show that each estimated rate has substantial uncertainty. The unadjusted p-value of 0.031 is one statistical summary of the comparison, not a measure of the probability that either treatment is effective or ineffective.

The result does not establish how long responses lasted, whether participants lived longer, or whether progression was delayed. Those questions relate to other outcomes, including the secondary outcomes named in the registry, whose detailed results are not included in the listed summary. A response-rate endpoint also does not capture every dimension of disease status or participant experience.

The registry describes randomized Phase II arms, which is relevant to interpreting a treatment comparison, but its design fields are not fully consistent: allocation is marked randomized and the model is labeled single group. The registry also allows crossover at the treating physician’s discretion after progressive disease. The available record does not explain the primary analysis population or how crossover and missing assessments were handled. These limits make it difficult to attribute the entire observed contrast specifically to the addition of cyclophosphamide from the registry summary alone.

General statistical interpretation separates the estimate, its uncertainty, and the study’s design. The response rates describe what was recorded in the study arms; the intervals indicate sampling precision; and the p-value reflects a test under specified assumptions. None of these alone resolves questions about bias, analysis choices, or generalizability. The record does not report enough information to make those assessments comprehensively, and the findings should not be treated as medical advice.

16. Why This Trial Matters Statistically

This trial illustrates why an arm-level percentage should be interpreted together with its confidence interval and the comparison method. The observed response rates are visibly different, but the estimates have broad intervals. A point estimate alone can make the precision appear greater than it is, while an interval helps readers recognize the range of values compatible with the data and method.

It also highlights the distinction between a randomized comparison and the record’s account of the design. Randomized allocation is listed, yet the model is labeled single group, and the study includes Phase I dose escalation, randomized Phase II arms, and a crossover pathway. These features make it especially important to identify which participants and treatment assignments contribute to a particular endpoint. The primary outcome is explicitly restricted to Phase II participants, but further analysis-population detail is not reported in the registry record.

The p-value is unadjusted and appears alongside several outcomes, while the multiplicity plan is not reported. This is a useful reminder that a nominal test result does not automatically account for the broader set of questions examined in a trial. Sample-size illustrations based on the observed effect also answer a different question from the original design calculation, which is not reported.

Finally, safety counts require context. Serious-event counts are reported for groups of different sizes, including a crossover group, and the registry does not report exposure duration or event-level detail. Statistical reading therefore involves more than comparing numbers: it requires attention to the endpoint definition, analysis population, uncertainty, design, and reporting limits.

17. Limitations

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

The registry record contains design descriptions that are not fully aligned. It identifies randomized allocation and no masking, while the model field says single group. The arm descriptions include Phase I dose escalation, randomized Phase II arms, and a crossover arm. The record does not explain this combination of entries or provide the detailed randomization procedure.

The primary result is reported for the Phase II response endpoint, but the analysis population and handling of missing or unevaluable response assessments are not reported in the registry record. The relationship between the planned enrollment of 80 and the reported Phase II arm sizes is not explained. The record also does not state how crossover participants were treated in the primary analysis, or how response assessments after crossover were classified.

The statistical analysis plan, including covariate adjustment, multiplicity handling, and prespecified decision criteria, is not reported. Although the registry names progression-free survival, overall survival, and possibly related adverse events as secondary outcomes, detailed results for those outcomes are not included in the listed summary. Follow-up details and analysis methods for time-to-event outcomes are not reported either.

Safety information is presented as counts by group, but the record does not specify exposure duration, the full event definitions, grading procedures, or the denominator for the listed serious-event term percentages. Death counts are not reported in the registry record. These reporting limits prevent a full assessment of safety rates or event attribution from the counts alone.

These are limitations of what can be established from the registry record, not evidence that the study did not collect or analyze additional information. More complete reporting would be needed to assess the robustness of the comparison, the handling of crossover and missing data, and the interpretation of secondary outcomes.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Pomalidomide in Combination With High Dose Dexamethasone and Oral Cyclophosphamide — NCT01432600.
• Registry record last updated 2017-05-23; status last verified 2017-02.
• Results first posted 2017-05-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

The registry describes a completed Phase I and Phase II study of pomalidomide with high-dose dexamethasone, with oral cyclophosphamide included in some regimens, in myeloma. The sponsor is H. Lee Moffitt Cancer Center and Research Institute. The record lists a start date of 2011-11, primary completion of 2016-08, and planned enrollment of 80.

The primary Phase II outcome is overall response rate, defined as minimal remission or better using the stated International Myeloma Working Group criteria over 36 Months. Reported rates are 38.9% for pomalidomide and dexamethasone and 64.7% for that regimen with cyclophosphamide. The record also lists progression-free survival, overall survival, and possibly related adverse events as secondary outcomes.

The record identifies randomized allocation but labels the model single group and describes crossover after progressive disease. Detailed analysis methods, missing-data handling, and the original sample-size justification are not reported in the registry record.