Panobinostat, Gemcitabine Hydrochloride, Busulfan, and Melphalan Before Stem Cell Transplant in Treating Patients With Refractory or Relapsed Multiple Myeloma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Panobinostat, Gemcitabine Hydrochloride, Busulfan, and Melphalan Before Stem Cell Transplant in Treating Patients With Refractory or Relapsed Multiple Myeloma (NCT02506959), a randomized phase 2 study. The primary outcome is Progression Free Survival (PFS).

2. Clinical Question

The primary endpoint is the number of participants alive and disease free one year after transplant. The question is framed around two transplant settings rather than two distinct conditioning regimens: the registry describes the first cohort as receiving a first autologous transplant and the second as receiving a second autologous transplant, with panobinostat and Gem/Bu/Mel in both.

The study is registered as a phase II trial with randomized allocation and a parallel model. However, the registry record does not explain how randomization was applied to the two cohorts, whether it concerned another aspect of the study, or how the allocation process related to first versus second transplant. The posted results therefore support a descriptive comparison of the cohorts, but they do not by themselves clarify the causal interpretation of that comparison.

The study enrolled 83 participants: 50 in the first-transplant cohort and 33 in the second-transplant cohort. The primary measure is a count at a specified follow-up time, rather than a time-to-event estimate. The available results address that count and an unadjusted cohort comparison; they do not establish that observed differences are due to the transplant setting or regimen.

3. Trial Design

This is a phase II study listed as randomized, with a parallel model and no masking. The registry identifies M.D. Anderson Cancer Center as the sponsor and reports the study status as completed. Enrollment was 83. The posted cohort descriptions distinguish participants receiving a first autologous transplant from those receiving a second autologous transplant.

Both cohorts received panobinostat by mouth once daily on days -9 to -2, gemcitabine hydrochloride intravenously over 4 hours on days -8 and -3, busulfan intravenously over 3 hours on days -8 to -5, and melphalan intravenously over 30 minutes on days -3 and -2. Each cohort then underwent autologous peripheral blood stem cell transplant on day 0. The posted regimen is therefore the same in both cohorts, while the transplant setting differs.

The record gives 50 participants for the first-transplant cohort and 33 for the second-transplant cohort. Although allocation is listed as randomized, how randomization was implemented, what was randomized, and whether it determined cohort membership are not reported in the registry record. The protocol’s original sample-size justification and original design assumptions are also not reported in the registry record. The planning illustrations associated with the posted results are separate from that original trial-design information.

The primary outcome is the number of participants alive and disease free one year after transplant. Secondary outcomes listed include overall survival up to 2 years and participants who experienced grade 3 or higher adverse events. The record contains results for overall survival and adverse events, but a detailed statistical plan, analysis populations, handling of missing outcome data, and interim-analysis procedures 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:

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 Progression Free Survival (PFS), measured over 1 year.

The primary endpoint is progression-free survival at one year, expressed in the registry as a count: the number of participants who were alive and disease free one year after autologous transplant. In this record, the measure is not presented as a median duration or as a hazard ratio. It is a status at a specified time, summarized by the number meeting the endpoint among the participants in each cohort.

This kind of endpoint is used to describe whether participants have both remained alive and avoided disease progression by a meaningful follow-up point. Combining survival and disease status in a single measure can represent more of the clinical course than either status alone. It is important, however, to read the registry’s specific definition: the posted primary result is a one-year count, and it does not provide details on the timing of progression events or how disease status was assessed.

The record reports 38 participants meeting the endpoint among 50 in the first-transplant cohort and 24 among 33 in the second-transplant cohort. An unadjusted comparison is also posted. These summaries describe the outcomes recorded for the two cohorts; they do not establish why participants differed or whether cohort membership caused any difference.

Details such as the assessment schedule, rules for classifying disease progression, and handling of participants whose one-year status was unavailable are not reported in the registry record. Those omissions matter when interpreting a fixed-time count, because a reader cannot determine from the registry entry alone how incomplete follow-up or endpoint classification may have affected the reported totals.

7. Results Posted in the Registry

• Cohort 2_2nd Auto TP Conditioned With Panobinostat and Gem/Bu/Mel: 72.7% (24/33) versus 76.0% (38/50) on control; risk difference -3.3 percentage points (95% CI -22.5 to 16.0), risk ratio 0.96 (0.74–1.24); unadjusted two-proportion z-test p = 0.737.

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.

Overall Survival (OS)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cohort 2_2nd Auto TP Conditioned With Panobinostat and Gem/Bu/Mel: 48.5% (16/33) versus 54.0% (27/50) on control; risk difference -5.5 percentage points (95% CI -27.5 to 16.4), risk ratio 0.90 (0.58–1.39); unadjusted two-proportion z-test p = 0.623.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort 2_2nd Auto TP Conditioned With Panobinostat and Gem/Bu/Mel and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists overall survival and participants experiencing grade 3 or higher adverse events as secondary outcomes. The overall-survival results follow the same broad descriptive pattern as the primary comparison: the posted unadjusted cohort contrast is numerically lower for the second-transplant cohort. The registry does not include a reported analysis for that secondary outcome, so the result should not be treated as a confirmatory finding or as a separate basis for a strong conclusion.

The overall-survival outcome is related to, but not interchangeable with, the primary endpoint. The primary result counts participants alive and disease free at one year, whereas overall survival records participant survival over a follow-up period of up to 2 years. The distinction matters: a participant can be alive without being disease free, and the follow-up windows differ. The endpoints therefore capture different aspects of outcome and cannot be combined into a single summary from the registry information.

The adverse-event endpoint provides a safety perspective rather than an efficacy comparison. The posted adverse-event summaries include serious events, other events, and deaths, while the listed secondary outcome refers specifically to participants with grade 3 or higher adverse events. The registry does not report a detailed statistical analysis connecting those summaries to that endpoint.

Unadjusted secondary results carry less weight because they are not accompanied by a reported multiplicity plan, a complete analysis plan, or documented adjusted comparisons. When multiple outcomes are examined, the chance of at least one apparently notable result can increase if no adjustment or prespecified hierarchy is used. The registry record does not state whether such procedures were planned. The secondary results are therefore best understood as descriptive context that complements, but does not independently confirm, the primary finding.

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

• Overall Survival (OS)
• Participants Who Experienced Grade 3 or Higher Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

A risk difference expresses the difference between the proportions of participants meeting a binary outcome in two groups. For this comparison, the groups are the second-transplant cohort and the first-transplant cohort, and the event is being alive and disease free at one year. The reported estimate is -0.033. Its negative direction means the observed proportion was lower in the second cohort than in the first under the calculation used. This is an unadjusted comparison based on the posted counts; it does not account for other participant or clinical characteristics.

A risk difference is measured on the proportion scale. It describes an absolute contrast between group outcome proportions, rather than how many times as likely one group is to have the outcome. It can be useful because it is directly tied to the frequency of the outcome in each cohort. But without adjustment or a design description that explains how the cohorts were formed, the estimate remains a comparison of the recorded groups, not necessarily a causal effect.

How should the interval and p-value be read?

The registry comparison gives an interval from -0.225 to 0.160 for the risk difference. In general, an interval estimate conveys a range of values reasonably compatible with the observed data under the statistical method used. A narrower interval indicates more precision, while a wider interval indicates less precision. The interval’s precise confidence level and calculation method are not reported in the registry record, so they should not be assumed.

The unadjusted p-value is 0.737. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It does not give the probability that the null hypothesis is true, and it does not measure clinical importance. A large p-value is not evidence that the groups are equivalent. Equivalence requires a prespecified margin and a design and analysis suited to that question; those details are not reported in the registry record.

Why are these results unadjusted?

The posted comparison is an unadjusted re-calculation from the summary counts. Such a calculation uses the numbers meeting the endpoint and the group totals without incorporating additional covariates. It can summarize the crude difference between the observed cohorts, but it cannot correct for differences in prognosis or other factors between people in the first- and second-transplant settings.

The registry lists randomized allocation, but the relationship between that designation and the two reported cohorts is not explained. Because the cohort descriptions distinguish transplant history, it would be inappropriate to assume that participants were randomly assigned between those cohort types. The allocation procedure, any stratification, and any adjusted analysis are not reported in the registry record. Consequently, the comparison should be interpreted in light of that uncertainty.

What is over-dispersion, and does it apply?

In general, over-dispersion means that observed variability is greater than a statistical model expects. It can matter for outcomes modeled as counts or rates, because underestimated variability can make intervals too narrow and tests too optimistic. The primary endpoint is recorded as a binary participant count at one year, not as a repeated count or event rate. The registry does not report an over-dispersion assessment or a model-based analysis. It is therefore not appropriate to claim that over-dispersion was tested or addressed.

What does the secondary analysis record contain?

Overall survival is recorded as a secondary outcome with follow-up up to 2 years. The registry posts group counts and an unadjusted comparison, but lists no reported analyses for that outcome. The comparison can be read as a descriptive, summary-statistic calculation, not as a documented sponsor analysis. The secondary safety outcome is participants who experienced grade 3 or higher adverse events, but the registry’s posted adverse-event summaries do not provide a detailed statistical comparison for that endpoint.

Across these analyses, the registry does not report the full statistical analysis plan, missing-data methods, analysis populations, or adjustment for multiple outcomes. General statistical principles can explain what the reported quantities mean, but they cannot fill in those unreported procedures. Interpretation should therefore remain anchored to the observed counts and the explicitly posted unadjusted estimates.

11. Confidence Intervals and Precision

The primary cohort comparison has a risk-difference estimate of -0.033 and an interval from -0.225 to 0.160. In general, an interval describes uncertainty around an estimate under a specified statistical procedure. The range extends from a potentially appreciable negative difference to a positive difference, so the posted estimate is not precise enough to distinguish confidently among those possibilities. The confidence level and method used for the interval are not reported in the registry record.

The ratio summaries also span values on both sides of their null value. The risk ratio is 0.957, with an interval from 0.737 to 1.242. The odds ratio is 0.842, with an interval from 0.308 to 2.298. These intervals likewise do not isolate a single direction of association. They offer alternate scales for describing the same cohort comparison, but do not remove the limitations of an unadjusted comparison between different transplant settings.

For overall survival, the risk difference is -0.055, with an interval from -0.275 to 0.164. Its risk ratio is 0.898, with an interval from 0.581 to 1.387, and its odds ratio is 0.802, with an interval from 0.332 to 1.934. These secondary estimates are also imprecise. The posted results do not report interval methods or confidence levels, so no specific coverage level should be inferred.

Precision depends on the amount of information in the data and the variability of the outcome. The cohort sizes are 50 and 33, and the broad ranges of the posted intervals reflect substantial uncertainty in the estimated comparisons. An interval crossing the no-difference value is not proof of no effect; it indicates that the data and method do not tightly locate the difference. Larger or more informative studies could yield narrower estimates, but their results cannot be predicted from these data alone.

12. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not the trial’s original sample-size justification. For these binary outcomes, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

For the primary comparison, the row planning for 100% of the observed effect lists 2,793 participants per arm for 80% power and 3,739 participants per arm for 90% power. The row planning for 75% of the observed effect lists 4,914 and 6,578 participants per arm, respectively. The row planning for 50% of the observed effect lists 10,938 and 14,642 participants per arm, respectively.

In plain terms, 80% power means that, under the planning assumptions and for the chosen effect, a study of that size would have an 80% chance of detecting the specified effect using the stated significance threshold. The 90% column describes a higher chance of detection under the same assumptions, which requires a larger planned sample. The illustrations also show that smaller effects need more participants to detect.

These figures are not observed power and do not describe the probability that the completed trial’s conclusion is correct. They are hypothetical planning quantities calculated from the observed effect, which may itself be uncertain. They should not be read as evidence that the original trial was designed to those sample sizes or assumptions.

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 = 0.760; treatment proportion p₁ = 0.727; average p̄ = 0.744.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6175 = 1.2102.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6170 = 0.5193.
4. n = (1.2102 + 0.5193)² / (-0.0327)² = 2,792.9, rounded up to 2,793 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 <- 0.76                          # control proportion
p1 <- 0.727272727272727                          # 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(2506959)
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 = 2,793 (80% power), 3,739 (90% power)
 75% of observed effect: n per arm = 4,914 (80% power), 6,578 (90% power)
 50% of observed effect: n per arm = 10,938 (80% power), 14,642 (90% power)
power.prop.test: 2792.9 
Simulated power at n = 2,793 per arm: 0.798 (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

Multiplicity arises when a study evaluates more than one outcome, comparison, subgroup, or time point. In general, looking across many statistical tests without a prespecified strategy can increase the chance of a misleading positive finding. A protocol may address this with an outcome hierarchy, adjusted significance thresholds, or other prespecified procedures. Whether any such approach was planned or used is not reported in the registry record.

The registry lists one primary outcome and two secondary outcomes. The primary endpoint is a one-year count of participants alive and disease free. Overall survival is listed up to 2 years, and the other secondary outcome concerns participants who experienced grade 3 or higher adverse events. The record does not describe a multiplicity adjustment or explain whether the secondary outcomes were intended as confirmatory or exploratory.

Missing-data handling is also not reported in the registry record. The posted primary counts give the number meeting the endpoint and the cohort totals, but do not explain how participants with unavailable one-year status were handled, whether follow-up was complete, or whether any imputation or censoring rules were applied. Those details can affect interpretation of a fixed-time count.

The analysis populations are not reported in the registry record. It is not specified whether the results include all enrolled participants, only participants who received transplant, or another defined set. The record also does not describe exclusions after enrollment, adherence to the assigned or planned regimen, or how protocol deviations were handled.

Interim analyses, stopping rules, and the full statistical analysis plan are not reported in the registry record. These omissions do not invalidate the posted counts, but they limit assessment of how the results were selected, analyzed, and interpreted. The registry’s unadjusted comparisons should be read as summaries of the posted data rather than as a complete account of the prespecified trial analysis.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: viral (12.1%), fungal (6.1%), pulmonary edema (4.0%), ast increased (3.0%), creatinine increased (3.0%).

The adverse-event summaries report serious events in 2 of 50 participants in the first-transplant cohort and 4 of 33 in the second-transplant cohort. Other adverse events are reported for 47 of 50 and 30 of 33 participants, respectively. Deaths are listed for 23 participants in the first cohort and 17 in the second. These are separate registry summaries; the record does not establish from these counts alone whether every event category is mutually exclusive or how the timing of events relates to follow-up.

The registry lists viral events at 12.1%, fungal events at 6.1%, pulmonary edema at 4.0%, AST increased at 3.0%, creatinine increased at 3.0%, and diarrhea at 3.0% among the top serious-event terms. The record does not explain the denominator or event-counting rules behind each listed percentage, so the terms should be read as reported rather than converted into participant counts.

These figures describe safety events recorded in the registry; they do not, on their own, establish that the regimen caused an event or permit a reliable comparison of safety between cohorts. Definitions, event-collection methods, follow-up duration for safety, and a statistical comparison are not reported in the registry record.

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

The posted results describe outcomes among participants in two transplant settings who received the same panobinostat and Gem/Bu/Mel conditioning regimen. The primary endpoint records how many participants were alive and disease free one year after transplant. The unadjusted comparison has a negative point estimate for the second-transplant cohort, but its interval spans differences in either direction. The available data therefore do not precisely establish the direction or size of a cohort difference.

This is not a comparison of the regimen with an alternative treatment or with no treatment. Nor does the registry entry make clear how randomization related to membership in the first- and second-transplant cohorts. The observed contrast could reflect differences associated with transplant history, participant characteristics, or other factors not described in the posted results. The comparison should not be interpreted as showing that transplant setting caused the observed pattern.

The p-value does not prove that there is no difference, and the interval does not prove equivalence. Conversely, the point estimate alone is not evidence of a meaningful benefit or harm. Statistical uncertainty, the cohort structure, and missing methodological details all constrain what can be concluded.

The secondary outcome summaries provide additional descriptive information about survival and adverse events. They do not replace the primary endpoint, and their interpretation is limited by the absence of reported analysis details and a stated approach to multiple outcomes. The safety counts describe reported events but do not determine whether those events were caused by the regimen.

Overall, the registry record is best read as a report of observed counts and unadjusted comparisons in a phase II study. It does not provide enough information to make a causal claim, assess the full analysis strategy, or generalize the numerical results beyond the studied cohorts. It is a statistical description of the posted data, not medical advice.

17. Why This Trial Matters Statistically

This trial is statistically informative because its registry entry puts a fixed-time binary endpoint alongside two clinically distinct transplant cohorts. That makes the choice of estimand important: the primary result is a count of participants alive and disease free at one year, while the comparison contrasts a first transplant with a second transplant. The contrast is not between two conditioning regimens.

The record also illustrates why an interval estimate matters alongside a point estimate and p-value. The risk-difference estimate is close to zero on the proportion scale, but the interval is broad and crosses zero. A reader who considers only the point estimate could overstate how well the cohort difference is known; a reader who considers only the p-value could incorrectly conclude that no difference exists. Together, these statistics indicate substantial uncertainty in the unadjusted comparison.

Another statistical issue is the distinction between randomized allocation as recorded and the groups actually compared. The registry labels the study randomized, yet the posted cohorts are defined by first versus second transplant. Without a description of randomization, analysts cannot assume that the cohort comparison inherits the protections of random assignment. Clear reporting of allocation and analysis populations would help readers assess this distinction.

The planning illustrations further distinguish study-design questions from post-result calculations. They show how hypothetical sample requirements vary with the effect assumed, but they do not reveal the original justification for the enrolled sample. This is a useful reminder that a planning calculation based on an observed estimate is not evidence of the trial’s design intent or its observed power.

Finally, the record makes visible the importance of reporting multiplicity, missing-data procedures, and endpoint definitions. Without these details, even accurately reported counts have limited interpretive reach. Statistical relevance comes not only from a numerical result, but also from knowing which question was planned and how the data were analyzed.

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.

A key limitation is that the two reported cohorts differ by transplant setting: one is a first autologous transplant and the other a second. The registry does not report participant characteristics or an adjusted analysis that would help assess whether the groups were otherwise comparable. The unadjusted cohort contrast therefore cannot isolate the effect of transplant history or any other factor.

Although allocation is listed as randomized, the registry record does not explain what was randomized or how allocation relates to cohort membership. It would be unsafe to assume that the first- and second-transplant cohorts were randomized against each other. The absence of that explanation limits causal interpretation of their comparison.

The primary endpoint is a count at one year, but endpoint assessment details and handling of missing status are not reported. Analysis populations, exclusions, adherence, and follow-up completeness are also not reported in the registry record. These details would help establish exactly whom the counts represent and how participants without complete outcome information were treated.

The comparison intervals’ confidence level and calculation method are not reported. The full statistical analysis plan, multiplicity procedures, interim analyses, and original sample-size rationale are also not reported. Secondary outcomes have limited analysis detail, and the adverse-event summaries do not explain event-collection rules or the denominator behind the listed serious-event percentages.

Finally, the sample-size illustrations use the observed effect for planning and should not be treated as the study’s original design calculations. The total enrollment of 83 and the cohort sizes offer limited information for estimating differences precisely, as reflected in the broad posted intervals. These limitations constrain interpretation without changing the fact that the registry reports the stated counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Panobinostat, Gemcitabine Hydrochloride, Busulfan, and Melphalan Before Stem Cell Transplant in Treating Patients With Refractory or Relapsed Multiple Myeloma — NCT02506959.
• Registry record last updated 2025-03-18; status last verified 2025-02.
• Results first posted 2025-03-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed phase II trial of panobinostat with gemcitabine hydrochloride, busulfan, and melphalan before autologous stem cell transplant for refractory or relapsed myeloma. It lists randomized allocation, no masking, a parallel model, and enrollment of 83 participants. The posted cohorts are a first-transplant group of 50 and a second-transplant group of 33, both receiving the same conditioning regimen.

The primary outcome is the number alive and disease free one year after transplant. The registry also lists overall survival and grade 3 or higher adverse events as secondary outcomes. Posted primary results include an unadjusted cohort comparison with a broad interval, while the registry record does not report the full analysis plan, missing-data approach, analysis populations, or multiplicity procedures.

The results are descriptive of the two posted cohorts and do not establish a causal difference between transplant settings or a treatment effect against an alternative regimen. The planning illustrations are not the trial’s original sample-size justification or observed power.