Stem Cell Transplantation in Individuals With Multiple Myeloma (BMT CTN 0102): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Stem Cell Transplantation in Individuals With Multiple Myeloma (BMT CTN 0102) (NCT00075829), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS).

2. Clinical Question

3. Trial Design

BMT CTN 0102 is registered as a phase III, multi-center trial of transplant strategies for multiple myeloma. The registry lists randomized allocation and no masking, and describes a crossover model. It records enrollment of 710 and a completed status. The recorded start is 2003-12 and primary completion is 2012-06. These are registry entries and do not, by themselves, describe the full conduct or follow-up of the trial.

The design description distinguishes two features. Patients were biologically assigned to the transplant strategy according to whether an HLA-matched sibling was available: the strategy with two autologous transplants or the strategy with an autologous transplant followed by a matched-sibling non-myeloablative allogeneic transplant. Within the tandem autologous strategy, the registry describes a nested randomized phase III comparison of observation with maintenance therapy after the second autologous transplant. The registry record does not report how these assignment procedures were implemented beyond that description.

The reported primary endpoint is progression-free survival at year 3, defined as a percentage among patients who completed the second transplant. The record presents results separately for standard-risk and high-risk groups, and includes comparisons of auto-auto with auto-allo within each group. The endpoint population restriction matters: the reported primary outcome is not explicitly described as an analysis of every enrolled participant.

The arm descriptions specify one year of either observation or dexamethasone and thalidomide maintenance after the second autologous transplant, and one year of observation after the auto-allo strategy. The registry lists secondary outcomes including overall survival, progression or relapse, treatment-related mortality, time between transplants, and graft-versus-host disease. Numerical results are posted for some, but not all, of those outcomes. The registry record does not report the original sample-size justification or detailed statistical analysis plan.

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: Patients that completed second transplant

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: Analysis is based on intention-to-treat data. Primary analysis of the clinical trial focused on patients meeting protocol criteria of standard risk multiple myeloma.

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS), measured over Year 3.

The primary endpoint is progression-free survival (PFS) at year 3, reported as a percentage of patients. The registry defines failure as death, progression, or relapse. PFS therefore combines disease progression or relapse with death: it describes the proportion who have not experienced any of those defined failures by the specified time point, as represented in the registry’s percentage measure.

This type of endpoint is used to capture disease control while also counting death as an event, rather than describing relapse alone. That makes its interpretation different from overall survival, which concerns survival, and from cumulative incidence of progression or relapse, which focuses on disease events. The endpoint can be clinically relevant to trial questions about disease control, but the registry’s definition and analysis population must remain attached to the result.

The registry specifies that the PFS population consists of patients who completed the second transplant. It reports year-3 percentages and 95% confidence intervals separately for standard-risk and high-risk groups and for the auto-auto and auto-allo strategies. The reported percentage is not a raw event count, and it should not be read as applying automatically to everyone enrolled. The registry record does not report the method used to estimate PFS, the handling of censoring, or an adjusted analysis for this endpoint. Those details affect how a time-to-event endpoint is estimated and compared, so they cannot be inferred from the percentages alone.

7. Results Posted in the Registry

• Auto-Allo Standard Risk: 42.9% (67/156) versus 45.9% (168/366) on control; risk difference -3.0 percentage points (95% CI -12.2 to 6.3), risk ratio 0.94 (0.76–1.16); unadjusted two-proportion z-test p = 0.535.
• Auto-Auto High Risk: 32.3% (10/31) versus 45.9% (168/366) on control; risk difference -13.6 percentage points (95% CI -30.9 to 3.6), risk ratio 0.70 (0.42–1.18); unadjusted two-proportion z-test p = 0.142.
• Auto-Allo High Risk: 41.4% (12/29) versus 45.9% (168/366) on control; risk difference -4.5 percentage points (95% CI -23.2 to 14.1), risk ratio 0.90 (0.58–1.41); unadjusted two-proportion z-test p = 0.638.

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) for High Risk

• 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:
  • Auto-Allo High Risk: 58.6% (17/29) versus 67.7% (21/31) on control; risk difference -9.1 percentage points (95% CI -33.5 to 15.2), risk ratio 0.87 (0.59–1.28); unadjusted two-proportion z-test p = 0.464.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Auto-Allo High Risk and the control. The interval gives the range of effects that remain compatible with the data.

Cumulative Incidence of Progression/Relapse

• 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:
  • Auto-Allo Standard Risk: 46.2% (72/156) versus 50.0% (183/366) on control; risk difference -3.8 percentage points (95% CI -13.2 to 5.5), risk ratio 0.92 (0.76–1.13); unadjusted two-proportion z-test p = 0.421.
  • Auto-Auto High Risk: 58.1% (18/31) versus 50.0% (183/366) on control; risk difference 8.1 percentage points (95% CI -10.0 to 26.2), risk ratio 1.16 (0.85–1.59); unadjusted two-proportion z-test p = 0.389.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Auto-Allo Standard Risk 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 Auto-Auto High Risk and the control. The interval gives the range of effects that remain compatible with the data.

Cumulative Incidence of Treatment Related Mortality (TRM)

• 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:
  • Auto-Allo Standard Risk: 10.9% (17/156) versus 4.1% (15/366) on control; risk difference 6.8 percentage points (95% CI 1.5 to 12.1), risk ratio 2.66 (1.36–5.19); unadjusted two-proportion z-test p = 0.003.
  • Auto-Auto High Risk: 9.7% (3/31) versus 4.1% (15/366) on control; risk difference 5.6 percentage points (95% CI -5.0 to 16.2), risk ratio 2.36 (0.72–7.72); unadjusted two-proportion z-test p = 0.152.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Auto-Allo Standard Risk than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Auto-Auto High Risk and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context to the primary PFS result by examining survival, progression or relapse, and treatment-related mortality. They measure related but distinct aspects of outcome. Overall survival concerns survival, progression or relapse focuses on disease events, and treatment-related mortality concerns a safety outcome. None should be treated as a substitute for the primary endpoint, and a pattern in one outcome does not automatically determine the pattern in another.

Across the posted secondary results, estimates do not all point in the same direction or carry the same precision. The high-risk overall-survival and progression/relapse comparisons have wide intervals that include no difference. The standard-risk treatment-related mortality comparison has an interval that excludes zero in the recalculated unadjusted analysis, whereas the high-risk treatment-related mortality interval includes zero. These results provide additional descriptive evidence but do not alter the definition or interpretation of the primary endpoint.

The registry lists further outcomes, including standard-risk overall survival, interval from first to second transplantation, and incidences of acute and chronic graft-versus-host disease. Numerical results for these are not reported in the registry record among the posted outcome results summarized for this analysis. Their absence limits how comprehensively the overall benefit-and-risk pattern can be assessed from the registry.

Secondary comparisons usually carry less weight than a prespecified primary analysis because many outcomes and subgroups create multiple opportunities for apparently notable results. The registry record does not report whether these secondary comparisons were prespecified, how multiplicity was addressed, or what adjustment strategy was used. Their unadjusted p-values therefore should be treated as exploratory evidence rather than as independent confirmation. The clinical and statistical interpretation should consider outcome definitions, precision, design, and completeness of reporting together.

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

• Overall Survival (OS) for Standard Risk
• Overall Survival (OS) for High Risk
• Cumulative Incidence of Progression/Relapse
• Cumulative Incidence of Treatment Related Mortality (TRM)
• Interval From First to Second Transplantation
• Incidences of Graft Versus Host Disease (GVHD)
• Incidences of Chronic GVHD

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes use percentages, confidence intervals, and comparisons expressed as risk differences. Understanding what each measure represents helps keep descriptive results distinct from conclusions about treatment effects. The comparison calculations are identified as recalculated and unadjusted; the registry record does not report a corresponding set of sponsor analyses in its analysis listing.

What does a percentage describe?

For these binary percentage outcomes, the value is the reported percentage of participants with the relevant event or endpoint status at the stated time. For PFS, the registry reports the percentage meeting the endpoint definition and identifies death, progression, or relapse as failures. For secondary outcomes such as progression or relapse and treatment-related mortality, the reported percentage refers to the named outcome. These measures are not interchangeable: PFS incorporates the specified failure definition, whereas progression or relapse and treatment-related mortality refer to different outcomes.

Arm percentages are descriptive summaries. They do not by themselves account for differences in baseline characteristics, follow-up, censoring, or the way participants entered a risk stratum. The record’s description of biological assignment based on matched-sibling availability is especially relevant when considering whether observed arm differences can be attributed solely to transplant strategy. The nested maintenance comparison is described as randomized, but the results discussed for the primary comparison concern auto-auto and auto-allo transplant strategies.

What is a risk difference?

A risk difference expresses the difference between the percentages in two groups, on the probability scale. Its sign depends on which group is subtracted from which; the comparison label is therefore essential. A risk difference of zero corresponds to equal event probabilities on that scale. The confidence interval expresses uncertainty around the estimated difference. If it includes zero, the posted summary statistics are compatible with no difference as well as with differences in either direction, subject to the assumptions of the calculation.

The recalculated comparisons use the posted arm summaries and are unadjusted. They should not be confused with a model-based or covariate-adjusted analysis. The registry record does not report an adjusted treatment effect, a method for accounting for time-to-event data, or the analysis details needed to reproduce a sponsor’s primary analysis. The fact that an unadjusted p-value is available does not supply those missing details.

How should a p-value be read?

A p-value describes how incompatible the observed data are with a specified null model, assuming that model and the calculation’s assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The p-values accompanying recalculated comparisons are unadjusted. A small value on its own does not resolve limitations in assignment, endpoint estimation, or multiplicity; a larger value does not prove that groups are equivalent.

In this record, several outcomes and risk groups are listed, and multiple comparisons can be made. Without the analysis plan and multiplicity approach, a single unadjusted p-value cannot be read as if it were the only planned test. The registry record does not report whether the displayed contrasts were prespecified or whether any formal adjustment for multiple testing was used.

Why do confidence intervals matter?

A confidence interval gives a range of values compatible with the data under the method used to construct it. It conveys precision as well as direction. A narrow interval indicates greater precision than a broad one, while an interval spanning zero for a risk difference leaves a wider range of possible group differences unresolved. A confidence interval is not a guarantee that the true value lies within its endpoints, and it does not address bias from study design or analysis choices.

The arm-level confidence intervals and the recalculated comparison intervals answer related but different questions. The first quantify uncertainty around each arm’s percentage; the second quantify uncertainty around a between-arm difference. Their endpoints should not be compared as a substitute for the interval on the difference itself.

What is not available in the registry record?

The registry record does not report the original sample-size justification, detailed analysis plan, handling of missing outcomes, censoring rules, interim analyses, or multiplicity procedure. It also does not report a statistical method for estimating the year-3 PFS measure. These omissions prevent a full reconstruction of the trial’s intended analysis. General statistical principles can explain how intervals and unadjusted comparisons work, but they cannot fill in trial-specific methods that are not reported.

11. Confidence Intervals and Precision

The confidence intervals show that precision varies by risk group and outcome. For standard-risk PFS, the arm estimates are 46.0% with a 95% confidence interval from 42.0% to 51.0% for auto-auto, and 43.0% with a 95% confidence interval from 36.0% to 51.0% for auto-allo. The recalculated difference interval, from -0.122 to 0.063, includes zero and allows for a range of possible differences in either direction.

For high-risk PFS, the arm confidence intervals are 22.0% to 50.0% for auto-auto and 27.0% to 60.0% for auto-allo. These intervals are broad, and the comparison interval from -0.232 to 0.141 also includes zero. The small high-risk arm denominators recorded for this endpoint, 31.0 and 29.0, accompany less precise estimates than the standard-risk arm denominators, 366.0 and 156.0. This is consistent with the general principle that smaller samples often produce more uncertainty, though precision also depends on event patterns and the analysis method.

Confidence intervals describe sampling uncertainty under the method used; they do not account for potential selection effects, errors in outcome classification, or incomplete reporting. Overlap between arm-level intervals is not a formal test of the difference, so the interval for the contrast is the more direct measure for that question. The registry record does not report how the primary endpoint intervals were constructed, which limits a fuller assessment of their statistical properties.

The secondary high-risk overall-survival comparison has a broad interval, from -0.335 to 0.152, while the standard-risk treatment-related mortality contrast has an interval from 0.015 to 0.121. These intervals express different levels of precision and should be interpreted outcome by outcome. Precision does not establish clinical importance, and an interval’s width does not determine whether an effect is meaningful in practice.

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 comparison effects, not the trial’s original design assumptions. For these binary outcomes, the figures are participants per arm. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects at 100%, 75%, and 50% of the observed effect. Smaller effects require more participants to detect under the same planning assumptions.

The 80% power column gives the illustrative participants per arm for a design that would have an 80% chance of detecting the stated effect under the assumed model and significance level, if that effect were the true effect. The 90% power column describes the corresponding planning target with a 90% chance under those same assumptions. These are design calculations, not probabilities that the observed result is correct, and they do not tell whether a completed study had enough power after seeing its results.

For example, planning at a smaller fraction of the observed effect yields larger per-arm requirements than planning at the full observed effect. This reflects a general statistical principle: distinguishing a subtler difference from random variation generally requires more information. The figures are not adjusted for trial-specific features that are not reported in the registry record, such as a detailed attrition assumption or an analysis model.

The listed sample-size figures are not observed power. The registry record does not report the trial’s original sample-size rationale or detailed design assumptions, so these illustrations should not be taken as a reconstruction of the planned enrollment or as a retrospective assessment of the trial’s adequacy.

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 = 0.459; treatment proportion p₁ = 0.429; average p̄ = 0.444.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7027 = 1.3773.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7024 = 0.5911.
4. n = (1.3773 + 0.5911)² / (-0.0295)² = 4,443.5, rounded up to 4,444 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 <- 0.459016393442623                          # control proportion
p1 <- 0.429487179487179                          # 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(75829)
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 = 4,444 (80% power), 5,949 (90% power)
 75% of observed effect: n per arm = 7,914 (80% power), 10,594 (90% power)
 50% of observed effect: n per arm = 17,833 (80% power), 23,873 (90% power)
power.prop.test: 4443.5 
Simulated power at n = 4,444 per arm: 0.797 (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 examines several outcomes, subgroups, or comparisons. Each additional statistical test creates another opportunity for a result to appear notable by chance, even when no real group difference exists. This concern is relevant to BMT CTN 0102 because results are presented across risk groups and the registry lists multiple secondary outcomes. It does not mean that any particular finding is false; it means that isolated unadjusted results require cautious interpretation alongside the full analysis plan.

The registry record does not report a multiplicity procedure or say whether the subgroup contrasts and secondary endpoints were prespecified. It also does not provide a detailed statistical analysis plan. As a result, the posted unadjusted p-values cannot be interpreted as adjusted confirmatory tests, and it is not possible to establish from the registry whether any endpoint had a formal priority after the primary outcome.

Missing-data methods are also not reported in the registry record. The primary endpoint is defined for patients who completed the second transplant, but the record does not explain how patients who did not complete that transplant were handled, whether outcome status was available for all members of the stated endpoint population, or how missing observations were treated. The results should therefore be read with the stated analysis population in mind; they cannot automatically be generalized to all enrolled participants.

The registry record also does not report censoring rules or the method used to estimate year-3 PFS. For a time-related endpoint, follow-up duration and censoring can affect estimates, so the percentage alone does not reveal the full analysis. Interim analyses, stopping rules, and the trial’s original sample-size justification are not reported in the registry record either. These omissions do not invalidate the posted values, but they constrain independent assessment of the planned analysis, the handling of incomplete follow-up, and the strength of confirmatory claims.

15. 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 .2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: thrombocytopenic purpura (2.7%), mucosal inflammation (2.7%), graft versus host disease (2.7%), fever (2.7%), cerebrovascular accident (2.7%).

The registry reports serious and other adverse-event counts by risk and transplant group. For serious adverse events, the recorded affected and at-risk counts are 15 and 436 for auto-auto standard risk, 10 and 189 for auto-allo standard risk, 2 and 48 for auto-auto high risk, and 5 and 37 for auto-allo high risk. For other adverse events, the affected counts are 1, 1, 0, and 0, respectively, with the same at-risk counts recorded for those groups.

These are registry adverse-event summaries, not the year-3 outcome denominators used for PFS. The record does not report deaths in the adverse-event listing. The most frequently listed serious-event terms each have a reported value of 2.7%: thrombocytopenic purpura, mucosal inflammation, graft versus host disease, fever, cerebrovascular accident, and convulsion. The record does not clarify whether individuals could contribute to more than one term, so the terms should not be treated as mutually exclusive or summed.

Adverse-event counts describe what was recorded in the registry and do not by themselves establish that an event was caused by a transplant strategy. Comparisons also require attention to the groups’ different denominators and to the registry’s incomplete reporting of analytic methods. The record does not report further detail about event definitions or severity grading beyond the serious and other categories presented.

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

The posted results describe year-3 outcome percentages and uncertainty in groups defined by transplant strategy and risk category. For the primary endpoint, the standard-risk arm estimates are close in magnitude, while the high-risk arm estimates are imprecise. The recalculated unadjusted PFS comparison intervals include zero. These findings do not establish a clear difference in PFS between the strategies, but neither do they demonstrate equivalence.

The result also does not establish that the strategies have identical effects in standard-risk and high-risk patients. The subgroup estimates have different precision, and the registry does not report a formal test of interaction. Subgroup percentages should therefore remain descriptive rather than be interpreted as proof that risk category changes the relative effect.

Secondary outcomes provide additional information but do not answer the primary question on their own. Some comparisons show different patterns from PFS, and the registry does not report multiplicity handling or detailed analysis methods. Those findings are not a reason to replace the primary endpoint with a secondary result. They should be considered as part of a broader assessment of outcomes, uncertainty, and the limits of registry reporting.

The registry describes biological assignment to the transplant strategies based on availability of an HLA-matched sibling, alongside a nested randomized maintenance comparison. That design description matters when interpreting associations between the transplant strategy and outcome. The unadjusted recalculations do not account for potential differences between biologically assigned groups and should not be presented as definitive causal estimates.

These data do not establish an individual treatment choice, and they do not provide medical advice. They report outcomes for the specified registry populations and time point. The registry record does not provide all methods needed to evaluate how estimates were generated, how missing outcomes were handled, or how multiple comparisons were addressed. Interpretation should remain bounded by those limitations and by the reported endpoint population of patients who completed the second transplant.

17. Why This Trial Matters Statistically

This trial raises several statistical issues that are common in complex clinical studies. Its registry description combines a transplant-strategy comparison based on matched-sibling availability with a nested randomized maintenance comparison. That distinction matters: labels such as “randomized” do not alone describe how every comparison was assigned. Interpreting estimates requires attention to the assignment mechanism for the specific contrast.

The primary endpoint is reported only for patients who completed the second transplant. That restriction makes the analysis population central to interpretation. A result among patients meeting that condition does not automatically describe everyone enrolled, and the registry record does not report how those who did not complete the transplant were handled in the endpoint analysis.

Risk-stratified reporting also illustrates a precision challenge. The standard-risk endpoint groups have larger recorded denominators than the high-risk groups, and the high-risk intervals are broad. Subgroup estimates can be informative, but small subgroup samples make it difficult to distinguish modest differences from random variation. A visible numerical gap between point estimates is not enough to establish a subgroup effect.

Finally, multiple outcomes and comparisons create a multiplicity problem, while the absence of a detailed analysis plan makes it difficult to determine which findings were confirmatory. The registry’s posted secondary results can help describe the broader outcome pattern, but unadjusted comparisons should not be treated as a collection of independent definitive tests. This trial is a useful example of why study design, analysis population, precision, and reporting completeness must be considered together.

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.

Several trial-specific limitations affect interpretation of the registry results. The primary endpoint population is described as patients who completed the second transplant. The registry record does not report how many otherwise eligible participants did not complete it, how they were handled analytically, or whether missing endpoint data occurred among those included. Consequently, the displayed PFS percentages cannot be assumed to represent all enrolled participants.

The registry describes biological assignment to auto-auto or auto-allo according to matched-sibling availability. The recalculated comparisons are unadjusted and do not address potential differences associated with that assignment mechanism. The record does not report adjusted estimates or enough detail to assess the comparability of the groups on prognostic factors.

Results are presented separately for standard-risk and high-risk groups, but the registry record does not report a formal interaction analysis or explain whether subgroup comparisons were prespecified. The high-risk primary-endpoint groups have small recorded denominators and broad confidence intervals, limiting precision. In addition, the comparison calculation uses the auto-auto standard-risk arm as the stated control for all posted primary contrasts; that means some high-risk recalculated contrasts are not direct within-risk comparisons. The arm-specific percentages should not be mistaken for a formal risk-stratum comparison.

The registry record does not report the original sample-size justification, detailed statistical analysis plan, PFS estimation method, censoring rules, missing-data approach, interim analyses, or multiplicity procedure. The secondary outcome results are also incomplete relative to the listed outcomes. These reporting gaps limit independent evaluation of the intended analyses and the strength of conclusions that can be drawn from the posted summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Stem Cell Transplantation in Individuals With Multiple Myeloma (BMT CTN 0102) — NCT00075829.
• Registry record last updated 2021-11-01; status last verified 2017-08.
• Results first posted 2016-08-04.
• 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.

22. Record Summary

BMT CTN 0102 is a completed phase III, multi-center multiple myeloma transplant trial with registry enrollment of 710. The registry describes biological assignment between tandem autologous transplantation and autologous followed by matched-sibling non-myeloablative allogeneic transplantation, with a nested randomized maintenance-versus-observation comparison in the tandem autologous strategy.

The primary endpoint is year-3 PFS among patients who completed the second transplant, with failure defined as death, progression, or relapse. Results are separated by standard-risk and high-risk groups. The posted percentages and recalculated unadjusted comparison intervals do not establish a clear PFS difference. Selected secondary results provide additional outcome information, but they are unadjusted and incompletely reported across the listed outcomes.

The registry record does not report the original design assumptions or detailed statistical methods needed for a complete reconstruction of the analysis. Interpretation should account for the specified endpoint population, biological assignment, subgroup precision, and missing information on multiplicity and missing-data handling.