Panobinostat/Bortezomib/Dexamethasone in Relapsed or Relapsed-and-refractory Multiple Myeloma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Panobinostat/Bortezomib/Dexamethasone in Relapsed or Relapsed-and-refractory Multiple Myeloma (NCT02654990), a randomized phase 2 study. The primary outcome is Overall Response Rate (ORR).

2. Clinical Question

The study compared three active regimens rather than a regimen with placebo or no panobinostat. Its main clinical question was therefore comparative: whether the observed response proportions differed among these dosing schedules in the enrolled population. The registry record identifies overall response rate as the primary outcome and specifies independent review according to International Myeloma Working Group criteria.

The primary response assessment covered up to 168 days. It counted confirmed partial response, immunophenotypic complete response, stringent complete response, complete response, or very good partial response. Best overall response was selected from confirmed post-baseline assessments recorded after randomization and before progressive disease, death, start of new therapy, withdrawal of consent, or end of study, whichever occurred first.

The trial also examined a longer-term overall response rate and several other secondary outcomes. Those outcomes address different aspects of response, disease course, survival, and drug exposure; they do not replace the primary comparison. Numerical findings available for the primary endpoint are the clearest basis for describing the randomized regimen comparisons.

3. Trial Design

This was a multicenter, randomized, open-label phase 2 study with a parallel, three-arm design. The registry record reports enrollment of 248 participants and completion status. Randomization assigned participants to one of three panobinostat schedules, each combined with subcutaneous bortezomib and oral dexamethasone. The study was not masked, while the primary response outcome was assessed by an independent review committee.

The regimens differed in panobinostat dose and frequency: 20 mg three times a week, 20 mg twice a week, or 10 mg three times a week. Each panobinostat regimen followed a 2-weeks-on/1-week-off schedule. The background treatment included bortezomib and dexamethasone. For participants aged 75 years or younger, the registry summary describes subcutaneous bortezomib twice weekly for 4 cycles and then weekly from Cycle 5 until disease progression. Participants older than 75 years were to receive it weekly throughout the treatment period.

Treatment was planned to continue until disease progression or earlier discontinuation for unacceptable toxicity or other reasons. Participants who stopped treatment for reasons other than progression were to continue efficacy follow-up every 6 weeks. Survival follow-up was planned until the last participant entering long-term follow-up had completed a 3-year follow-up period; the summary available in the registry record ends before completing that sentence, so further wording is not reported in the registry record.

The study began on 2016-04-27, and its primary completion date was 2019-10-18. The registry record describes prior exposure to immunomodulatory agents as part of the intended population. Detailed eligibility criteria, randomization procedures, allocation concealment, and the original design assumptions are not reported in the registry record. The available record also does not state the planned sample size for each arm or give the rationale for selecting the enrollment target.

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

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS): all participants to whom study treatment was assigned by randomization.

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: Full analysis set (FAS): all participants to whom study treatment was assigned by randomization.

6. Primary Endpoint

The registry lists the primary outcome as Overall Response Rate (ORR), measured over Up to 168 days.

The primary endpoint was overall response rate, expressed as the percentage of participants with a confirmed partial response or better as their best overall response after completion of up to 8 cycles of the assigned regimen. The response categories included partial response, immunophenotypic complete response, stringent complete response, complete response, and very good partial response. The assessment timeframe was up to 168 days, and each cycle was 21 days long.

Best overall response was based on confirmed post-baseline response assessments, stopping at the earliest of progressive disease, death, start of new therapy, withdrawal of consent, or end of study. The registry record specifies that an independent review committee assessed response blindly according to International Myeloma Working Group criteria. This distinction matters because the treatment itself was open-label: the endpoint review was described as blinded even though participants and study personnel were not masked.

Response rate is a binary outcome at the participant level: each participant either met the response definition or did not. It provides a direct summary of the proportion reaching a defined response threshold, rather than describing the depth or duration of response for every participant. That makes it useful for comparing response proportions across randomized regimens, while leaving other questions—such as how long responses last or how survival differs—to other outcomes. The registry record does not report the detailed statistical analysis plan for this endpoint.

7. Results Posted in the Registry

• Arm B - Panobinostat (20 mg, BIW): 65.1% (54/83) versus 62.2% (51/82) on control; risk difference 2.9 percentage points (95% CI -11.8 to 17.5), risk ratio 1.05 (0.83–1.32); unadjusted two-proportion z-test p = 0.702.
• Arm C - Panobinostat (10 mg, TIW): 50.6% (42/83) versus 62.2% (51/82) on control; risk difference -11.6 percentage points (95% CI -26.6 to 3.4), risk ratio 0.81 (0.62–1.07); unadjusted two-proportion z-test p = 0.133.

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.

ORR Throughout the Study

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B - Panobinostat (20 mg, BIW): 67.5% (56/83) versus 62.2% (51/82) on control; risk difference 5.3 percentage points (95% CI -9.3 to 19.8), risk ratio 1.08 (0.87–1.36); unadjusted two-proportion z-test p = 0.478.
  • Arm C - Panobinostat (10 mg, TIW): 53.0% (44/83) versus 62.2% (51/82) on control; risk difference -9.2 percentage points (95% CI -24.2 to 5.8), risk ratio 0.85 (0.65–1.11); unadjusted two-proportion z-test p = 0.233.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B - Panobinostat (20 mg, BIW) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C - Panobinostat (10 mg, TIW) and the control. The interval gives the range of effects that remain compatible with the data.

iCR Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B - Panobinostat (20 mg, BIW): 1.2% (1/83) versus 3.7% (3/82) on control; risk difference -2.5 percentage points (95% CI -7.1 to 2.2), risk ratio 0.33 (0.03–3.10); unadjusted two-proportion z-test p = 0.306.
  • Arm C - Panobinostat (10 mg, TIW): 1.2% (1/83) versus 3.7% (3/82) on control; risk difference -2.5 percentage points (95% CI -7.1 to 2.2), risk ratio 0.33 (0.03–3.10); unadjusted two-proportion z-test p = 0.306.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B - Panobinostat (20 mg, BIW) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C - Panobinostat (10 mg, TIW) and the control. The interval gives the range of effects that remain compatible with the data.

sCR Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B - Panobinostat (20 mg, BIW): 1.2% (1/83) versus 1.2% (1/82) on control; risk difference -0.0 percentage points (95% CI -3.4 to 3.3), risk ratio 0.99 (0.06–15.53); unadjusted two-proportion z-test p = 0.993.
  • Arm C - Panobinostat (10 mg, TIW): 3.6% (3/83) versus 1.2% (1/82) on control; risk difference 2.4 percentage points (95% CI -2.3 to 7.1), risk ratio 2.96 (0.31–27.91); unadjusted two-proportion z-test p = 0.317.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B - Panobinostat (20 mg, BIW) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C - Panobinostat (10 mg, TIW) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the assessment beyond the primary response evaluation after up to 8 cycles. The registry lists overall response rate throughout the study, separate response categories, progression-free survival, overall survival, and panobinostat maximum plasma concentration among its secondary measures. Numerical results available in the record include the longer-term overall response rate, immunophenotypic complete response rate, and stringent complete response rate. Numerical findings for the other listed outcomes are not reported in the registry record.

At a broad level, the longer-term overall response results retain the same ordering of arm estimates as the primary response assessment: the 20 mg twice-weekly arm has the largest reported proportion, followed by 20 mg three times weekly and then 10 mg three times weekly. The longer assessment period makes that secondary endpoint distinct from the primary assessment; it should not be treated as a replacement primary result or as independent confirmation of it. The separate complete-response categories describe smaller portions of the response profile and are based on sparse counts in the posted data.

These secondary results are best read as supporting context for the overall response pattern. They address outcomes related to, but not identical with, the primary endpoint. A longer follow-up window can capture responses occurring after the primary assessment period, while response-category measures distinguish depth rather than simply whether the overall response threshold was reached. Survival outcomes would address other questions, but their numerical results are not reported in the registry record.

Unadjusted secondary comparisons carry less weight because several endpoints and arm contrasts create multiple opportunities for apparently notable findings. The registry record does not report a multiplicity plan, confirmatory hierarchy, or adjusted secondary analyses. Thus, the secondary results are descriptive signals, not a basis for treating any one finding as a conclusive treatment difference. Their value is in showing whether the overall pattern is coherent with the primary result and in identifying questions that would require prespecified, adequately powered evaluation.

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

• ORR Throughout the Study
• iCR Rate
• sCR Rate
• CR Rate
• VGPR Rate
• Progression-free Survival (PFS)
• Overall Survival (OS)
• Maximum Plasma Concentration (Cmax): Panobinostat

9. Statistical Interpretation

10. Statistical Methods Explained

What does a response proportion represent?

Overall response rate is a binary endpoint summarized as the percentage of participants who met the response definition. Each participant contributes to the numerator if their best confirmed response reached partial response or better, and to the denominator according to the stated analysis population. The registry defines that population as participants assigned treatment by randomization. The endpoint therefore describes the frequency of reaching a response threshold; it does not, by itself, describe how long response lasted or the full pattern of disease change.

The primary measure combines several response categories, from partial response through the specified complete-response categories. Combining categories can make the endpoint easier to compare as a single proportion, but it also means that the overall percentage does not reveal how the responses were distributed among those categories. The registry lists separate response-category outcomes as secondary measures.

How should the risk difference be read?

General statistical explanation: a risk difference subtracts one group's event proportion from the other group's event proportion. A value of zero corresponds to equal proportions. A positive or negative value indicates the direction of the estimated difference according to the order of comparison. The recalculated comparisons use the 20 mg three-times-weekly arm as the reference. Thus, the reported risk difference of 0.029 for 20 mg twice weekly is positive, whereas -0.116 for 10 mg three times weekly is negative.

The difference estimates are presented on the proportion scale, while the arm results are presented as percentages. No conversion is needed to understand direction: the sign indicates which estimate is higher under the comparison's stated ordering. The confidence interval gives a range of values compatible with the data and calculation method, subject to the assumptions behind that method. When an interval includes zero, the data do not rule out equal proportions under that interval-based comparison.

What does a confidence interval communicate?

General statistical explanation: a confidence interval conveys uncertainty about an estimated quantity. A narrower interval indicates greater precision than a wider interval for the same kind of estimate. An interval is not a list of the most likely values, nor does it guarantee that the true value lies inside the particular interval. Its interpretation depends on the statistical procedure and assumptions used to calculate it.

For an arm-specific response percentage, the reported intervals describe uncertainty around that arm's estimated response proportion. For a risk difference, the interval describes uncertainty around the contrast between two proportions. Those are related but distinct quantities. Comparing the arm-specific intervals informally is not a substitute for examining the interval for the difference itself. The recalculated risk-difference intervals are the relevant uncertainty summaries for the pairwise contrasts.

What does an unadjusted p-value say?

General statistical explanation: a p-value measures how incompatible the observed data are with a specified null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value should be interpreted together with the estimate, its confidence interval, the endpoint definition, and the analysis plan.

The comparison p-values are explicitly unadjusted recalculations. They do not reflect a reported sponsor analysis, and there is no registry-reported adjustment for considering multiple arm comparisons. The registry record does not report the planned hypothesis tests, test direction, or multiplicity strategy. The reported numerical p-values should therefore not be treated as a complete account of the trial's confirmatory inference.

Why does the analysis population matter?

The primary outcome definition names the full analysis set and defines it as everyone to whom study treatment was assigned by randomization. This connects the endpoint to randomized assignment rather than to a subset defined by treatment completion. The registry record does not detail how missing endpoint assessments, treatment discontinuation, or other post-randomization events were handled in the primary analysis. Those details can affect how a response proportion is estimated and how broadly the result applies to the randomized population.

The best-overall-response definition also sets boundaries for the assessments considered: post-baseline confirmed responses were used until a listed event or end of study. That rule helps specify which observations can contribute to the endpoint. However, it does not by itself explain how absent assessments were classified or how participants without an evaluable response were treated. Those analytic rules are not reported in the registry record.

Why can over-dispersion matter?

General statistical explanation: over-dispersion arises when observed variation is greater than a statistical model expects. For binary endpoints, the variance and confidence interval depend on the model and on how the data are represented. In a simple comparison of participant-level proportions, the central issue is the observed counts and denominators; extra clustering or other dependence, if present, could require methods that account for it. The registry record does not report a clustering adjustment or a specific over-dispersion assessment, so none can be assumed for this study.

The methods information that is available is specific about the primary endpoint, its timeframe, the analysis population, and blinded independent response review. Detailed modeling choices, missing-data rules, covariate adjustment, and the statistical analysis plan are not reported in the registry record. Keeping those omissions visible is important: recalculations from the posted counts can clarify the scale and uncertainty of simple comparisons, but they cannot reconstruct unreported protocol decisions or replace the trial's own full analysis.

11. Confidence Intervals and Precision

The arm-specific 95% confidence intervals indicate meaningful uncertainty around each primary response estimate. For the 20 mg three-times-weekly regimen, the estimate is 62.2% with an interval from 50.8% to 72.7%. For 20 mg twice weekly, the estimate is 65.1% with an interval from 53.8% to 75.2%. For 10 mg three times weekly, the estimate is 50.6% with an interval from 39.4% to 61.8%. These intervals should be read as uncertainty around each arm's response proportion, not as direct intervals for differences between arms.

The recalculated risk-difference interval for 20 mg twice weekly versus 20 mg three times weekly ranges from -0.118 to 0.175. For 10 mg three times weekly versus 20 mg three times weekly, it ranges from -0.266 to 0.034. Both intervals include zero and extend to values on either side of it. This means the posted summaries are compatible with a range of pairwise differences, including no difference, under the recalculation method.

General statistical explanation: precision is about the width of an uncertainty interval, not whether its point estimate is favorable or unfavorable. A confidence interval that includes a value of no difference does not prove that the groups are equal. It indicates that the data and calculation do not sharply distinguish that value from other values inside the interval. The trial's modest arm sizes, as reported for this endpoint, are relevant context for interpreting the breadth of uncertainty, though the record does not report a formal precision target.

The independent committee's blinded response assessment is a feature of endpoint ascertainment, not a guarantee of narrow uncertainty. The intervals remain the way to judge how precisely the response proportions and their recalculated contrasts are estimated. No clinical threshold for a meaningful difference is reported in the registry record, so statistical uncertainty cannot be translated into a claim about whether any difference would be important to patients or clinicians.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the original trial design. For binary outcomes such as response rate, the figures are participants per arm. The planning assumptions listed for these calculations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. Time-to-event outcomes, if considered in these planning displays, use total events instead; the primary response outcome is not a time-to-event endpoint.

The 80% power column gives the number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column expresses the corresponding planning target for a 90% chance. These are design concepts, not guarantees about what a future study would find. For example, for the primary comparison between the 20 mg twice-weekly and 20 mg three-times-weekly regimens, planning for 100% of the observed effect gives 4,425 participants per arm for 80% power and 5,923 participants per arm for 90% power.

The calculations also show scenarios using 75% and 50% of the observed effect. Smaller effects require more participants to detect under the same assumptions, so the planning numbers rise as the assumed effect becomes smaller. The observed effect is used only as the starting point for these hypothetical scenarios; it is not a reliable promise that a future study will reproduce that effect.

This is not observed power. The trial's own original sample-size assumptions and justification are not reported in the registry record. These planning figures should not be read as evidence that the completed trial was designed to achieve any particular power for its primary or secondary comparisons.

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 = 0.622; treatment proportion p₁ = 0.651; average p̄ = 0.636.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6803 = 1.3334.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6800 = 0.5723.
4. n = (1.3334 + 0.5723)² / (0.0287)² = 4,424.4, rounded up to 4,425 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 <- 0.621951219512195                          # control proportion
p1 <- 0.650602409638554                          # 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(2654990)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 4,425 (80% power), 5,923 (90% power)
 75% of observed effect: n per arm = 7,900 (80% power), 10,575 (90% power)
 50% of observed effect: n per arm = 17,847 (80% power), 23,891 (90% power)
power.prop.test: 4424.4 
Simulated power at n = 4,425 per arm: 0.802 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The study had three randomized regimens, allowing more than one pairwise comparison, and the registry lists multiple primary and secondary outcome measures. Testing several contrasts or outcomes increases the chance of at least one seemingly notable result arising by chance when each is considered without adjustment. General statistical explanation: multiplicity procedures control or otherwise address that increased chance, often by changing how tests are interpreted or by specifying a hierarchy of hypotheses. The registry record does not report whether such a procedure was planned or used.

The unadjusted p-values associated with the recalculated primary comparisons do not account for multiple comparisons. The registry does not provide a reported analysis for those contrasts, and it does not specify a testing hierarchy, a family of hypotheses, or an adjustment method. Secondary outcomes also have no reported multiplicity adjustment. This makes the comparisons exploratory in interpretation, even where a numerical estimate and interval can be calculated from the posted summaries.

Missing-data handling is another key uncertainty. The primary endpoint names the full analysis set, defined as all participants assigned study treatment by randomization, but does not explain how missing response assessments were handled. The record does not report whether participants without an evaluable response were counted as nonresponders, excluded from a particular calculation, or managed using another method. It also does not state how incomplete follow-up or treatment discontinuation affected the primary estimate.

The endpoint definition specifies that confirmed post-baseline responses were considered until progressive disease, death, start of new therapy, withdrawal of consent, or end of study, whichever came first. That supplies a response-assessment boundary but not a complete missing-data policy. The registry record does not report interim analyses, covariate adjustment, the detailed statistical analysis plan, or the original sample-size justification. These omissions limit reconstruction of the intended inferential framework and should not be filled in by assuming common trial conventions.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 4.9% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (13.3%), pyrexia (4.8%), sepsis (4.8%), thrombocytopenia (3.8%), diarrhoea (3.8%).

The registry reports serious adverse event counts for participants at risk in each arm. The counts affected by at least one serious adverse event were 44 of 78 in the 20 mg three-times-weekly arm, 40 of 83 in the 20 mg twice-weekly arm, and 36 of 80 in the 10 mg three-times-weekly arm. These are counts, not exposure-adjusted rates. The numbers at risk differ from the primary full analysis set denominators, so the endpoint populations should not be conflated.

The most frequently listed serious event term was pneumonia at 13.3%. Other listed terms were pyrexia and sepsis at 4.8% each, and thrombocytopenia, diarrhoea, and lower respiratory tract infection at 3.8% each. The record also lists deaths of 34, 41, and 47 in the respective arms. These counts alone do not establish cause, timing, attribution to treatment, or comparative risk.

Serious adverse events are not the same as all adverse events. The record reports other adverse events affecting 78 of 78 participants in the first arm, 82 of 83 in the second, and 78 of 80 in the third. The posted counts need to be interpreted using their stated risk populations and event definitions. Detailed event-specific duration, severity breakdowns, exposure time, and causal assessments are not reported in the registry record.

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

The posted primary results describe confirmed response proportions for three panobinostat schedules used with bortezomib and dexamethasone in a randomized phase 2 study. The proportions differ numerically, with the 20 mg twice-weekly arm highest and the 10 mg three-times-weekly arm lowest. Recalculated unadjusted pairwise risk-difference intervals include zero, indicating that the posted summaries do not precisely establish a difference between either comparison and the reference regimen.

That reading is not a declaration that the regimens are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty is sufficiently contained within that margin; such information is not reported in the registry record. Nor do the data establish superiority based solely on the numerical ordering of the point estimates. The intervals span a range of possible differences, and no threshold for a clinically meaningful difference is reported.

The outcome is overall response over a defined assessment period. It does not by itself determine response duration, progression-free survival, overall survival, quality of life, or the full balance of benefits and harms. The registry lists some of those outcomes, but numerical findings for several are not reported in the registry record. Adverse event counts are also not a complete comparison of safety, particularly without exposure-adjusted analyses or detailed attribution information.

The study population was described as participants with relapsed or relapsed-and-refractory multiple myeloma who had previously been exposed to immunomodulatory agents. The estimates therefore pertain to the trial population and its eligibility context. The registry record does not supply enough detail to judge how closely that population represents any particular group beyond the stated description.

Overall, the posted data support a descriptive account of response proportions and their uncertainty. They do not, on their own, settle comparative efficacy, equivalence, clinical importance, or the full safety profile. Those conclusions would require the complete prespecified analysis, fuller outcome reporting, and interpretation of the results in their clinical context.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares three dose-frequency schedules in a randomized parallel design rather than evaluating a single regimen against an inactive control. That design makes the central interpretation a comparison among active regimens. The observed response percentages offer a useful description of how the trial arms differed, while the recalculated risk-difference intervals show why point estimates alone can overstate certainty.

The distinction between the open-label treatment design and blinded independent response review is also important. Knowledge of assigned treatment can affect aspects of trial conduct, while blinded assessment can reduce the influence of that knowledge on the primary response classification. The registry record describes both features, so neither should be overlooked when assessing how the endpoint was measured.

The endpoint's definition makes explicit that response was confirmed, based on best overall response, and assessed under named response criteria. Those choices improve interpretability of the reported outcome, but the registry does not report the detailed missing-data rules or full statistical analysis plan. The result is a useful example of the difference between a clearly defined clinical outcome and a fully documented inferential plan.

Finally, the sample-size illustrations emphasize how strongly planning depends on the effect assumed. The calculations use the observed effect as a starting point and show that smaller target effects call for larger studies under the stated assumptions. They are not evidence of the completed trial's power or a substitute for its original design rationale, which is not reported in the registry record. Together, these features make careful separation of observed data, recalculated comparisons, and unreported design choices essential.

18. Limitations

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

The registry record offers primary response estimates and confidence intervals, but it does not report the sponsor's detailed statistical analysis or the original statistical analysis plan. The primary comparisons discussed from summary statistics are therefore unadjusted recalculations, not a substitute for a complete trial analysis. The record also does not report a multiplicity strategy for the several arms and outcomes.

The available endpoint description is specific about the response threshold, assessment window, analysis population, and independent review. It does not specify how missing response data, participants without an evaluable assessment, or treatment discontinuations were handled analytically. Although the full analysis set is defined, the record does not provide enough detail to reconstruct every participant's contribution to the posted response percentages.

The study was open-label, and the registry summary does not give detailed information about allocation concealment or the randomization procedure. Blinded independent review is described for the primary response endpoint, but that does not resolve questions about masking in other trial processes. The registry record does not report whether interim analyses took place or whether the comparisons were adjusted for baseline characteristics.

The available numerical results are also incomplete across the registered outcomes. Some secondary endpoints are listed without numerical findings in the record, and detailed safety information such as event duration, exposure-adjusted comparisons, and attribution is not reported. The serious-event counts should consequently be read as descriptive counts rather than a complete comparative safety analysis. The original sample-size justification and study-specific power assumptions are not reported, limiting assessment of how the enrollment target was chosen.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Panobinostat/Bortezomib/Dexamethasone in Relapsed or Relapsed-and-refractory Multiple Myeloma — NCT02654990.
• Registry record last updated 2024-07-12; status last verified 2024-07.
• Results first posted 2024-07-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT02654990 was a completed, randomized, open-label, parallel phase 2 study of three panobinostat regimens combined with subcutaneous bortezomib and oral dexamethasone in participants with relapsed or relapsed-and-refractory multiple myeloma previously exposed to immunomodulatory agents. The registry reports enrollment of 248 participants. The primary endpoint was independently reviewed overall response rate after up to 8 cycles, within a timeframe of up to 168 days.

Reported primary response proportions were 62.2% for 20 mg panobinostat three times weekly, 65.1% for 20 mg twice weekly, and 50.6% for 10 mg three times weekly. Recalculated unadjusted risk-difference intervals for comparisons with the 20 mg three-times-weekly arm include zero. The registry record does not report the original sample-size justification, full statistical analysis plan, missing-data rules, or multiplicity approach. The numerical results support a descriptive comparison but leave uncertainty about the size and interpretation of between-regimen differences.