Safety and Efficacy Studies of Panobinostat and Bicalutamide in Patients With Recurrent Prostate Cancer After Castration: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Studies of Panobinostat and Bicalutamide in Patients With Recurrent Prostate Cancer After Castration (NCT00878436), a randomized phase 1, phase 2 study. The primary outcome is Percentage of Patients Free of Progression and Without Symptomatic Deterioration.

2. Clinical Question

The trial’s central statistical contrast is between two panobinostat dose schedules given with bicalutamide. It therefore addresses differences associated with assignment to these combination regimens, rather than isolating the effect of panobinostat from the effect of bicalutamide. The registry lists the study as randomized, open label, and parallel-group, with phase I and phase II components. Its brief description identifies safety, dosing schedule, and efficacy as aims. The primary result is a percentage at a fixed follow-up time, while the listed secondary outcomes concern time to PSA progression and a 50% or greater PSA decline by 9 months. The registry record does not report a comparator arm receiving bicalutamide without panobinostat.

3. Trial Design

The registry describes a randomized, open-label, parallel-group phase I/II trial. Enrollment was 52, and the study status is completed. The listed study dates are a start in 2009-06 and primary completion in 2015-03. The sponsor is NYU Langone Health. The trial concerns recurrent prostate cancer after castration, also listed under prostate cancer and prostatic neoplasms.

Both arms received bicalutamide 50 mg orally every day on a continuous basis. They differed in the panobinostat dose and weekly schedule. Arm A used 40 mg three times per week for two consecutive weeks, followed by one week of rest in each 21-day cycle; the arm title gives 120 mg per week. Arm B used 20 mg three times per week over the same two-weeks-on, one-week-rest schedule; its title gives 60 mg per week. Arm B was marked closed to accrual. The brief summary states that, as of July 23, 2013, the remaining accrual slots were to be allocated to Arm A.

Open-label means the registry does not describe masking of treatment assignment. Parallel-group means participants were assigned to a regimen rather than crossing between the listed regimens. Randomization is reported, but the method used to generate assignments, conceal allocation, or manage the change in accrual is not reported in the registry record. The original sample-size justification and the trial’s planned statistical analysis are not reported in the registry record. The posted primary endpoint includes a restriction: only participants who completed two or more treatment cycles were assessed. The reasons for this restriction and the handling of participants who did not meet it 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

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 Percentage of Patients Free of Progression and Without Symptomatic Deterioration, measured over 9 months.

The primary endpoint is the percentage of participants free of progression and without symptomatic deterioration at 9 months. The registry describes progression as determined by PSA and/or metastases criteria, or by clinical progression. Imaging criteria include body CT using RECIST criteria 1.1 and bone scans. For bone progression, the record describes the appearance of at least 2 new bone metastases and confirmation of 2 additional bone metastasis on a subsequent scan 6-8 weeks later. Only participants who completed two or more treatment cycles were assessed for this endpoint.

A fixed-time percentage gives a direct description of the proportion meeting the endpoint at a specified follow-up time. It can be easier to interpret than a time-to-event summary when the clinical question concerns status at that particular point. The registry also lists time to PSA progression as a secondary outcome, which addresses a different aspect of follow-up. No posted analysis for that secondary outcome is included in the registry record.

The endpoint combines progression assessment with symptomatic deterioration, so it is broader than a PSA measure alone. Combining clinical and imaging criteria may capture progression identified through different routes, but interpretation depends on consistent assessment and complete follow-up. The registry record does not report details on endpoint adjudication, missing endpoint assessments, or whether assessors were independent of treatment assignment. The trial was open label, so masking of participants and study staff is not reported.

7. Results Posted in the Registry

• LBH 20mg: 10.0% (2/20) versus 23.8% (5/21) on control; risk difference -13.8 percentage points (95% CI -36.3 to 8.7), risk ratio 0.42 (0.09–1.92); unadjusted two-proportion z-test p = 0.240.

8. Statistical Interpretation

9. Statistical Methods Explained

For a binary endpoint, each participant is classified according to whether the specified outcome was met. The registry labels the primary outcome as a percentage of participants and identifies its meaning as a percentage with an event. In this trial the endpoint title describes being free of progression and symptomatic deterioration at 9 months; the interpretation should follow that endpoint definition rather than assume that a percentage represents tumor response or a different outcome. The displayed values are 24% for LBH 40mg and 9% for LBH 20mg.

What does a risk difference describe?

General statistical explanation: A risk difference subtracts one group’s event proportion from the other group’s proportion, with the sign depending on which group is treated as the reference. Here the comparison is labeled for LBH 20mg and gives a risk difference of -0.138. The comparison fields indicate the higher-dose group as the reference proportion, 0.238, and the lower-dose proportion, 0.1. The negative sign therefore describes a lower observed endpoint proportion in the lower-dose group under that contrast’s direction. These are unadjusted group comparisons; no covariate-adjusted estimate is posted.

The registry also lists relative measures, with a risk ratio of 0.42 and interval 0.092 to 1.923, and an odds ratio of 0.356 and interval 0.060 to 2.093. General statistical explanation: A risk ratio compares proportions as a ratio, while an odds ratio compares odds. They use different scales from the risk difference, and their magnitudes should not be read as interchangeable. Both posted intervals include the null value for their respective measures, just as the risk-difference interval includes zero. For a binary outcome, the choice of measure affects how the comparison is expressed, not the underlying observed participants.

How should the p-value be understood?

General statistical explanation: A p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The posted unadjusted p-value is 0.24. The registry record does not report whether this test was prespecified, whether other inferential tests were planned, or whether a multiplicity procedure was used.

What does a confidence interval add?

General statistical explanation: A confidence interval communicates uncertainty around an estimate under the method’s assumptions. The risk-difference interval, -0.363 to 0.087, includes zero and also extends in both directions from the point estimate. This means the posted data do not pin down the direction or size of the underlying difference precisely. A confidence interval is not a guarantee that the true effect lies within its bounds, nor does it account for every possible source of bias or missing data.

What affects the analysis population?

The registry states that only participants who completed two or more treatment cycles were assessed for the primary endpoint. This is a defined assessment restriction, but the record does not say whether the analysis otherwise followed randomized assignment, how many participants were excluded from this endpoint assessment, or how incomplete follow-up was handled. General statistical explanation: Restricting analysis to participants who meet a post-randomization condition can change the composition of the groups being compared. If the condition is related to prognosis or treatment experience, the resulting comparison may not retain all the advantages of randomization. The registry does not provide enough detail to determine whether or how that issue affected this result.

There are four outcome measures listed and two secondary outcomes, but the registry reports zero analyses. No detailed trial statistical plan, interim analysis plan, missing-data method, or adjustment for multiple testing is reported in the registry record. Those omissions limit what can be inferred about whether the posted comparison was the planned primary analysis and how it relates to other analyses that may have been intended. Randomization is reported, but its implementation and any stratification factors are not reported in the registry record.

The assessment criteria include PSA, imaging, and clinical progression. General statistical explanation: Multiple ways of identifying an endpoint can make an outcome clinically broader, but they also make standardized definitions and consistent assessment important. Open-label conduct can be relevant when assessment includes judgment-based elements. The registry record does not report blinding of endpoint assessors, independent review, or procedures used to resolve uncertain assessments.

10. Confidence Intervals and Precision

The central estimate for the risk difference is -0.138 for LBH 20mg relative to LBH 40mg. Its 95% confidence interval ranges from -0.363 to 0.087. The interval contains zero, so the posted data are compatible with no difference on the risk-difference scale. It also includes values favoring either direction. The point estimate alone should not be treated as a precise estimate of the difference between regimens.

General statistical explanation: A confidence interval is a range generated by a statistical procedure intended to capture the underlying parameter at its stated confidence level over repeated use of that procedure, assuming its model and sampling assumptions are appropriate. It describes sampling uncertainty, not all possible errors. It does not account automatically for selection, measurement problems, incomplete follow-up, or analysis choices.

The interval is broad relative to the point estimate, reflecting substantial uncertainty in this comparison. The primary endpoint denominators are 21 and 20 participants, and the registry restricts assessment to those completing two or more treatment cycles. The record does not report the number of participants with missing endpoint status or the reasons for any missing assessments, so the contribution of incomplete data to uncertainty cannot be assessed from the registry.

Other posted relative-effect intervals are also broad: the risk ratio interval is 0.092 to 1.923, and the odds ratio interval is 0.060 to 2.093. Each spans its measure’s null value. These measures use different scales and should be read separately. Collectively, they do not provide a precise basis for choosing one dose schedule over the other. The registry record does not report a prespecified threshold for a difference considered important, which further limits interpretation of the interval in practical terms.

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 participants across both arms and not total events. They are illustrations based on the observed risk-difference effect, not the original trial’s design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is set to the stated fraction of the observed effect.

For planning at 100% of the observed effect, the figures are 115 participants per arm for 80% power and 153 participants per arm for 90% power. At 75% of the observed effect, they are 221 participants per arm for 80% power and 295 participants per arm for 90% power. At 50% of the observed effect, they are 533 participants per arm for 80% power and 713 participants per arm for 90% power. These are alternative planning scenarios, not observed trial results.

General statistical explanation: Power is the probability that a specified design will detect a prespecified effect at the chosen significance level if that effect is the true one and the planning assumptions hold. The 80% and 90% columns therefore describe different target probabilities of detecting the assumed effect. The 90% target requires more participants per arm than the 80% target for each listed effect scenario. Smaller effects require more participants because they are harder to distinguish from sampling variation.

The calculations use the observed effect as their starting point, so they should be treated as planning illustrations rather than a proposal or confirmation of the trial’s original design. This is not observed power. The registry record does not report the trial’s original sample-size assumptions or justification. The figures should not be interpreted as evidence that the completed trial had a particular probability of success or that the assumed effect is reliable.

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 = 0.238; treatment proportion p₁ = 0.100; average p̄ = 0.169.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5300 = 1.0389.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5210 = 0.4385.
4. n = (1.0389 + 0.4385)² / (-0.1381)² = 114.4, rounded up to 115 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 <- 0.238095238095238                          # control proportion
p1 <- 0.1                          # 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(878436)
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 = 115 (80% power), 153 (90% power)
 75% of observed effect: n per arm = 221 (80% power), 295 (90% power)
 50% of observed effect: n per arm = 533 (80% power), 713 (90% power)
power.prop.test: 114.4 
Simulated power at n = 115 per arm: 0.812 (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 four outcome measures, including the primary nine-month percentage, and identifies two secondary outcomes: time to PSA progression and the number of patients achieving a 50% or greater PSA decline by 9 months of therapy. It reports zero analyses. The posted primary comparison has an unadjusted p-value of 0.24. Whether outcomes were prespecified in a protocol, which tests were planned, and whether any multiplicity adjustment was used are not reported in the registry record.

General statistical explanation: When researchers examine multiple outcomes, time points, or contrasts, the chance of at least one apparently unusual result can increase if each is tested separately. A prespecified testing strategy or adjustment can address some of this issue. Without a reported plan, the reader cannot determine how the primary test was positioned among other planned comparisons or whether the reported p-value accounts for other testing.

The primary outcome description states that only participants who completed two or more treatment cycles were assessed. The registry does not report how many randomized participants did not meet this condition, whether outcome status was available for everyone eligible for assessment, or how any missing data were handled. It also does not report imputation, censoring rules for the fixed-time percentage, sensitivity analyses, or reasons for missing assessments.

The analysis population is not otherwise described in the registry record. In particular, it is not reported whether participants were analyzed according to randomized assignment, whether exclusions occurred after randomization, or how participants who stopped treatment or changed treatment were handled. General statistical explanation: These details matter because analyzing only a subset of randomized participants can affect comparability between arms. The registry does not provide sufficient information to assess the extent of any such effect.

Interim analyses, stopping rules, and a detailed statistical analysis plan are not reported in the registry record. The record therefore supports a description of the posted endpoint figures and comparison, but not a full audit of planned versus reported analyses or the treatment of incomplete data.

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: thrombocytopenia (17.9%), syncope (10.7%), dehydration (8.3%), vomiting (7.1%), cardiac asystole (4.2%).

For serious adverse events, the registry lists 28 participants at risk in LBH 40mg, with 11 affected, and 24 at risk in LBH 20mg, with 5 affected. These are arm-level counts in the safety record. The registry also lists participants affected by other adverse events: 26 of 28 in LBH 40mg and 24 of 24 in LBH 20mg. These categories describe different adverse-event summaries and should not be combined or treated as mutually exclusive without further information.

The serious adverse-event terms listed most often include thrombocytopenia at 17.9%, syncope at 10.7%, dehydration at 8.3%, vomiting at 7.1%, cardiac asystole at 4.2%, and dizziness at 4.2%. The registry record does not state the event counts corresponding to each term or specify in the posted listing whether these percentages represent participants, events, or another denominator. They should therefore be read as reported percentages, not recalculated or assigned a denominator not described in the record.

Death counts are not reported in the registry record. The safety summaries are descriptive and do not, on their own, establish comparative risk or causation. The registry record does not report a statistical comparison of adverse-event rates or details such as severity grading, timing, or treatment relatedness for each event.

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

The posted primary result describes the proportion meeting the nine-month endpoint in each dose arm among the participants assessed: 24% in LBH 40mg and 9% in LBH 20mg. The unadjusted risk-difference estimate for LBH 20mg relative to LBH 40mg is -0.138, with a 95% confidence interval from -0.363 to 0.087 and p = 0.24. The estimate points toward a lower endpoint percentage in the lower-dose arm, but the uncertainty is substantial and the interval includes no difference as well as differences in either direction.

This does not establish that the two dose schedules are equivalent, nor does it establish a reliable difference between them. Equivalence or non-inferiority requires a defined margin and a suitable design and analysis; such a margin is not reported in the registry record. The p-value alone cannot determine whether a difference matters, and the record does not give a threshold for clinical importance.

The comparison is between two combination regimens. Both include bicalutamide and panobinostat, with different panobinostat schedules. Consequently, the posted contrast does not isolate panobinostat’s contribution or compare the combination against bicalutamide alone, placebo, or another treatment. The trial’s endpoint includes PSA, imaging, and clinical criteria and is assessed at 9 months; it should not be substituted for the listed secondary outcomes, such as time to PSA progression.

The endpoint denominators are 21 and 20, while enrollment is 52 and safety denominators are 28 and 24. The registry does not explain these different counts. Only participants completing two or more cycles were assessed for the primary endpoint, and the record does not report missing-data handling or a complete analysis population. These factors, along with the open-label design and unreported assessment procedures, constrain interpretation. The results describe the posted analysis; they do not establish outcomes for people outside the assessed trial groups or determine what would happen under different treatment conditions.

16. Why This Trial Matters Statistically

This trial illustrates the importance of separating a dose comparison from a treatment-versus-control question. Randomization is reported, and the arms differ in the panobinostat dose schedule, while both receive continuous bicalutamide. The resulting comparison concerns the two combinations as assigned. It cannot, by itself, answer whether adding panobinostat changes outcomes relative to bicalutamide alone.

It also shows why effect estimates and their precision should be read together. The posted percentages differ, and the risk-difference point estimate has a direction, but its confidence interval spans zero and extends in both directions. The p-value does not remove that uncertainty. For a small analyzed population, a visually distinct pair of percentages can still leave substantial uncertainty about the underlying contrast.

Endpoint definition is another central statistical issue. The primary outcome combines a fixed-time status with progression criteria based on PSA, imaging, and clinical assessment, and it excludes participants who did not complete two or more cycles from assessment. Understanding the population and measurement rules is necessary before treating the reported percentages as directly comparable outcome rates.

Finally, the registry gives a useful distinction between a trial’s observed result and a planning illustration. The participant-per-arm figures are derived from the observed effect under stated assumptions, not from the trial’s original design rationale. They highlight how planning requirements change when the target effect is smaller or the desired power is higher, but they do not establish the adequacy of the completed study. The original design assumptions and detailed analysis plan are not reported in the registry record.

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 primary endpoint is assessed only among participants who completed two or more treatment cycles. The registry record does not report how many participants failed to meet this criterion, why they did not complete the required cycles, or whether their endpoint status was otherwise known. If inclusion in the endpoint analysis is related to prognosis or treatment experience, the analyzed groups may differ in ways not addressed by the posted comparison.

The endpoint combines PSA, imaging, and clinical progression criteria. The registry does not report endpoint adjudication, assessor masking, or procedures for resolving disagreements. Because the trial is open label, the record does not establish that outcome assessment was independent of knowledge of treatment assignment. The registry also does not report missing-data methods, sensitivity analyses, or how incomplete nine-month follow-up was treated.

The primary outcome denominators, 21 and 20, differ from the enrollment total of 52, while safety denominators are 28 and 24. The registry record does not explain these count differences, so the relationship between enrolled, treated, assessed, and analyzed participants cannot be fully reconstructed from the posted information. The original sample-size justification, randomization details, and statistical analysis plan are also not reported in the registry record.

The study compares two panobinostat dose schedules with bicalutamide in both arms and has no listed bicalutamide-only comparison. Its findings therefore cannot identify the effect of panobinostat versus no panobinostat. The primary estimate is imprecise, and the record does not state a threshold for a clinically important difference. The posted record also reports no analyses for the secondary outcomes, so the primary comparison cannot be placed alongside results for those outcomes.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy Studies of Panobinostat and Bicalutamide in Patients With Recurrent Prostate Cancer After Castration — NCT00878436.
• Registry record last updated 2018-02-07; status last verified 2018-01.
• Results first posted 2017-12-04.
• 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 record describes a completed randomized, open-label, parallel-group phase I/II trial in recurrent prostate cancer after castration. Enrollment was 52. Both arms combined continuous bicalutamide 50 mg daily with panobinostat on a 21-day cycle, using either the 40 mg or 20 mg dose three times per week for two weeks followed by one week of rest. Arm B, the lower-dose schedule, was closed to accrual.

The primary outcome was the percentage free of progression and without symptomatic deterioration at 9 months. Only participants completing two or more treatment cycles were assessed. The posted arm values were 24% for LBH 40mg and 9% for LBH 20mg; the risk difference for the lower-dose arm relative to the higher-dose arm was -0.138, with a 95% confidence interval from -0.363 to 0.087 and an unadjusted p-value of 0.24. The registry record lists two secondary outcomes but reports zero analyses. It also posts serious and other adverse-event counts, while death counts are not reported in the registry record.