Low-Dose or High-Dose Conditioning Followed by Peripheral Blood Stem Cell Transplant in Treating Patients With Myelodysplastic Syndrome or Acute Myelogenous Leukemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Low-Dose or High-Dose Conditioning Followed by Peripheral Blood Stem Cell Transplant in Treating Patients With Myelodysplastic Syndrome or Acute Myelogenous Leukemia (NCT00322101), a randomized phase 3 study. The primary outcome is Overall Survival.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase III trial with no masking. The registry lists an enrollment of 25 and identifies Fred Hutchinson Cancer Center as the sponsor. The trial began in 2006-01, had primary completion in 2012-04, and is listed as completed. The registry record does not give the original sample-size justification or the statistical assumptions used to plan the trial.

The comparison was between nonmyeloablative conditioning and myeloablative conditioning, each followed by allogeneic peripheral blood stem cell transplantation. The nonmyeloablative arm description names fludarabine phosphate, low-dose total-body irradiation, and cyclosporine as part of graft-versus-host disease prophylaxis. The myeloablative arm description refers to two treatment groups: one involving fludarabine and busulfan, and another involving cyclophosphamide and busulfan. These regimen descriptions are incomplete in the registry record, so details beyond the named components are not reported there.

The primary outcome was overall survival at 2 years, recorded as a participant count. The posted arm counts are 6 of 12 for the nonmyeloablative arm and 6 of 11 for the myeloablative arm. The primary outcome note says that 2 patients in the nonmyeloablative arm did not receive transplant because of relapse and withdrawal of consent. The record does not state how those participants were included in the primary outcome analysis.

Progression-free survival, non-relapse mortality, donor cell engraftment, disease progression or relapse, and acute and chronic graft-versus-host disease were among the listed secondary outcomes. Results are posted for some, but not all, of these outcomes. The registry record lists no reported analyses for the secondary outcomes, and it does not describe an analysis plan, blinding of outcome assessment, or follow-up procedures beyond the timeframes stated for individual outcomes.

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: 2 patients in the nonmyeloablative arm did not receive transplant due to relapse and withdrawal of consent

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 Overall Survival, measured over At 2 years.

Overall survival is a clinically important endpoint because it concerns whether participants remain alive over a specified follow-up period, rather than measuring only a laboratory change or an intermediate event. In general, a survival endpoint can summarize the net consequences of disease and treatment over time. That general interpretation depends on how the endpoint is defined and analyzed.

For this trial, the primary outcome is labeled overall survival at 2 years and is reported in participants. The registry posts 6 for the nonmyeloablative arm and 6 for the myeloablative arm, with arm denominators of 12 and 11. It does not provide a fuller operational definition of the count, a time-to-event estimate, or a description of censoring and analysis populations. The posted comparison is therefore a comparison of the registry’s participant counts, not a detailed survival-curve analysis.

The primary endpoint is intended to address whether the conditioning strategies differ in survival at the stated follow-up point. However, the registry record does not explain how participants who did not receive transplant were handled. Its note identifies 2 such patients in the nonmyeloablative arm, due to relapse and withdrawal of consent. That information matters for interpreting the population represented by the outcome counts, but the analysis handling is not reported in the registry record.

7. Results Posted in the Registry

• Arm II (Myeloablative Regimen): 54.5% (6/11) versus 50.0% (6/12) on control; risk difference 4.5 percentage points (95% CI -36.3 to 45.4), risk ratio 1.09 (0.50–2.38); unadjusted two-proportion z-test p = 0.827.

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.

Progression-free Survival

• 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:
  • Arm II (Myeloablative Regimen): 45.5% (5/11) versus 58.3% (7/12) on control; risk difference -12.9 percentage points (95% CI -53.4 to 27.7), risk ratio 0.78 (0.35–1.74); unadjusted two-proportion z-test p = 0.537.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Myeloablative Regimen) and the control. The interval gives the range of effects that remain compatible with the data.

Donor Cell Engraftment

• 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:
  • Arm II (Myeloablative Regimen): 100.0% (11/11) versus 91.7% (11/12) on control; risk difference 8.3 percentage points (95% CI -7.3 to 24.0), risk ratio 1.09 (0.92–1.29); unadjusted two-proportion z-test p = 0.328.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Myeloablative Regimen) and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Disease Progression/Relapse

• 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:
  • Arm II (Myeloablative Regimen): 18.2% (2/11) versus 58.3% (7/12) on control; risk difference -40.2 percentage points (95% CI -76.2 to -4.1), risk ratio 0.31 (0.08–1.19); unadjusted two-proportion z-test p = 0.049.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm II (Myeloablative Regimen) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover different aspects of transplant outcomes, including progression-free survival, engraftment, disease progression or relapse, non-relapse mortality, and graft-versus-host disease. The posted results do not give a complete set of analyzed estimates for every outcome named in the registry. The pattern across the outcomes with results is not uniform, so no single secondary measure provides a consistent extension of the primary comparison.

These outcomes are related to, but not interchangeable with, overall survival. Engraftment describes donor-cell establishment, while progression-free survival and disease progression or relapse concern disease status over follow-up. Non-relapse mortality and graft-versus-host disease address other consequences of transplantation. A difference in one of these measures does not automatically imply a corresponding difference in overall survival, because each captures a different event or clinical process.

The primary result remains the central comparison because overall survival is identified as the primary outcome. The secondary results may help describe possible pathways or trade-offs, but they do not resolve the primary estimate’s imprecision. The registry record lists no reported analyses for the secondary outcomes and does not explain whether these comparisons were prespecified or how their multiplicity was handled.

As a general statistical point, examining multiple outcomes creates more opportunities for apparently notable findings to arise by chance. Unadjusted secondary results therefore carry less confirmatory weight than a prespecified primary analysis, particularly when the study has limited precision and no analysis plan is available in the registry record. The outcomes can generate questions for further study, but they should not be treated as independent confirmation of a treatment effect.

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

• Progression-free Survival
• Non-relapse Mortality
• Donor Cell Engraftment
• Incidence of Disease Progression/Relapse
• Incidence and Severity of Acute and Chronic Graft-vs-host Disease

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is a difference in proportions, expressed as a risk difference. In general, a risk difference subtracts the event proportion in one group from the event proportion in the comparison group. A value of zero corresponds to equal proportions; a positive or negative value indicates the direction of the difference according to the specified arm ordering. Here, the comparison is for the myeloablative arm relative to the nonmyeloablative arm. The estimate is 0.045, with a 95% confidence interval from -0.363 to 0.454.

What does a confidence interval communicate?

As a general statistical explanation, a confidence interval describes uncertainty around an estimate under the assumptions of the method used. A narrower interval indicates greater precision, while a wider interval indicates less precision. An interval that includes zero for a difference does not establish that the true difference is zero. It means the posted data do not rule out zero under that interval method, while also allowing other effects within the interval. The registry record does not give the method used to calculate the posted primary interval.

How should the p-value be read?

As a general concept, a p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of a statistical test. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. The posted unadjusted p-value for the primary comparison is 0.827. The registry record does not identify the test used or say whether this comparison was designated as the sole confirmatory analysis in a prespecified plan.

Why are relative measures also reported?

The risk ratio compares the event proportions as a ratio, while the odds ratio compares the odds of the event between arms. These measures express contrasts differently from a risk difference. In general, a ratio of one corresponds to equal values between groups; values on either side indicate the direction of the comparison. The posted risk ratio is 1.091, with a 95% confidence interval from 0.499 to 2.384. The posted odds ratio is 1.2, with a 95% confidence interval from 0.233 to 6.185. Both intervals are broad. The registry record does not report adjusted estimates or describe covariates used in any model.

What does the outcome format tell readers?

The primary outcome is reported as a number of participants, rather than as a time-to-event estimate. In general, a participant count is a direct summary of how many people meet a stated outcome definition, but it depends on clear definitions of the event, the analysis population, and the follow-up window. The primary title names overall survival at 2 years, but the registry does not further define the count or report a survival curve, hazard ratio, or censoring approach. Those details are not reported in the registry record, so the posted count comparison should not be read as a complete time-to-event analysis.

The primary outcome note records that 2 patients in the nonmyeloablative arm did not receive transplant because of relapse and withdrawal of consent. The arm result still lists 12 as its denominator. The record does not explain whether the outcome was analyzed by randomized assignment, whether participants who did not receive transplant were included in follow-up, or how any missing survival information was handled. These distinctions can affect what treatment effect an analysis represents.

Why can small arm sizes produce uncertainty?

As a general statistical point, estimates based on limited observations tend to be sensitive to the outcome of individual participants. This can yield broad confidence intervals and unstable relative measures. Random assignment supports a comparison by reducing systematic selection at allocation, but it cannot make a small dataset precise. The wide intervals for the posted primary comparison reflect substantial uncertainty about the size and direction of the underlying difference.

General statistical methods also distinguish prespecified primary analyses from exploratory or secondary comparisons. Prespecification helps clarify which outcome and analysis carry the main confirmatory weight. The registry record identifies the primary endpoint but does not report an analysis plan, the planned test, or a multiplicity strategy. The record also lists no reported analyses for the secondary outcomes. These omissions limit assessment of whether the posted comparisons correspond to the trial’s original statistical plan.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.045, and its 95% confidence interval runs from -0.363 to 0.454. The interval crosses zero, so the posted data are compatible with no difference as well as with differences in either direction. Its breadth indicates that the estimate is not precise. The point estimate should not be interpreted as a stable or definitive measure of the contrast between conditioning strategies.

The relative estimates also have substantial uncertainty. The risk ratio of 1.091 has a 95% confidence interval from 0.499 to 2.384, while the odds ratio of 1.2 has a 95% confidence interval from 0.233 to 6.185. The intervals include values on both sides of the no-difference value for a ratio. As a general statistical explanation, wide intervals indicate that the data do not pin down the magnitude of the effect closely; they do not prove that no effect exists.

Small arm sizes are consistent with this limited precision, though the registry record does not report a formal precision target or original sample-size justification. The primary outcome is expressed as participant counts, and the outcome definition and handling of participants who did not receive transplant are not fully described. Those reporting limitations make it harder to judge exactly which population and estimand the interval represents.

The unadjusted p-value of 0.827 is not a substitute for examining the estimate and its interval. It does not demonstrate equivalence, and the confidence interval does not rule out effects of potentially substantial size. The appropriate reading is that the posted primary comparison is inconclusive and imprecise, not that the arms have been shown to be the same.

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 trial’s original design assumptions. The registry record does not report the original sample-size justification or its planning assumptions. For the binary outcomes in these planning calculations, the figures are participants per arm, not total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect.

The 80% power column indicates the number of participants per arm that the stated planning method estimates would be needed to have an 80% chance of detecting the assumed effect if that effect were the true one, under the calculation’s assumptions. The 90% power column uses a higher chance of detecting that assumed effect, and therefore generally requires more participants per arm. These are design-planning concepts, not guarantees for a future study.

Rows that use 100% of the observed effect assume a future study aims to detect an effect as large as the one estimated in this trial. Rows using 75% or 50% of the observed effect assume smaller effects. Smaller effects are harder to distinguish from random variation, so the planning figures require more participants per arm. For example, the primary-outcome illustration lists 1,895 participants per arm for 80% power at 100% of the observed effect and 7,593 participants per arm at 50% of the observed effect. These are planning illustrations, not observed power.

The calculations depend on assumptions that may not match a future study or the trial’s original design. The registry record does not report the original justification, nor does it establish that the observed effect is a reliable estimate for planning. These figures are best read as demonstrations of how required sample size changes when the target effect changes, rather than as a recommended enrollment target.

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 = 0.500; treatment proportion p₁ = 0.545; average p̄ = 0.523.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7064 = 1.3845.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7056 = 0.5939.
4. n = (1.3845 + 0.5939)² / (0.0455)² = 1,894.3, rounded up to 1,895 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 <- 0.5                          # control proportion
p1 <- 0.545454545454545                          # 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(322101)
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 = 1,895 (80% power), 2,536 (90% power)
 75% of observed effect: n per arm = 3,372 (80% power), 4,514 (90% power)
 50% of observed effect: n per arm = 7,593 (80% power), 10,164 (90% power)
power.prop.test: 1894.3 
Simulated power at n = 1,895 per arm: 0.794 (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 registry identifies overall survival at 2 years as the primary outcome and lists several secondary outcomes. It does not report a multiplicity strategy, such as how inference across multiple outcomes or comparisons was controlled. The record also lists no reported analyses for the secondary outcomes. Consequently, it is not possible to determine from the registry record which secondary comparisons were prespecified, which were exploratory, or whether any adjustment for multiple testing was planned.

As a general statistical explanation, multiplicity matters when researchers assess several outcomes or conduct multiple comparisons. Without an appropriate plan, the chance of encountering at least one apparently unusual result can increase. This does not make a secondary result invalid, but it does mean its strength as confirmatory evidence depends on the study’s prespecification and analysis approach. Those details are not reported in the registry record.

Information about missing data and the primary analysis population is also limited. The primary outcome note says that 2 patients in the nonmyeloablative arm did not receive transplant because of relapse and withdrawal of consent. The registry does not state how they were handled in the overall survival analysis, whether they remained in the assigned group for analysis, or whether follow-up continued after they did not receive transplant. Missing outcome data, censoring, and the treatment of withdrawals are not described.

The registry record does not report whether the analysis followed intention-to-treat principles, whether there was a per-protocol analysis, or how participants were assigned to the reported outcome denominators. It does not provide a statistical analysis plan, interim-analysis details, or sample-size justification. These are limits on what can be assessed from the posted record; their absence does not establish that the trial lacked such procedures, only that they are not reported in the registry record.

Because population handling, missing-data procedures, and multiplicity methods are not reported, the posted unadjusted comparisons should be read as descriptive evidence with important analytical uncertainties. The record does not provide enough detail to assess whether the comparison estimates the effect of assignment to a conditioning strategy, the effect among participants who received transplant, or another target population.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: severe diarrhea due to gut gvhd (18.2%), thrombotic microangiopathy (9.1%), mucositis (9.1%), tachycardia and hypotenstion (8.3%).

The registry reports serious adverse events affecting 3 participants at risk in the nonmyeloablative arm and 4 participants at risk in the myeloablative arm. Other adverse events were reported for 12 participants at risk in the nonmyeloablative arm and 11 at risk in the myeloablative arm. These are participant counts; they do not by themselves describe the number of separate events, their duration, or their severity beyond the serious-versus-other categorization.

The registry lists serious adverse event terms including severe diarrhea due to gut GVHD at 18.2%, Thrombotic Microangiopathy at 9.1%, Mucositis at 9.1%, and tachycardia and hypotenstion at 8.3%. The record does not provide enough context in these term listings to establish the arm attribution, event timing, or whether participants could contribute to more than one term. Deaths are not reported in the registry record.

These figures describe events recorded in this trial; they should not be used alone to rank the regimens’ safety. The arm sizes are limited, and the registry does not report detailed exposure time, event definitions, severity grading rules, or a statistical comparison of adverse events. Differences in counts can therefore be difficult to separate from uncertainty and reporting details.

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

The registry record documents a randomized comparison of nonmyeloablative and myeloablative conditioning followed by allogeneic peripheral blood stem cell transplantation. For the primary outcome labeled overall survival at 2 years, the posted participant counts are 6 in each arm. The unadjusted risk-difference estimate is 0.045, with a 95% confidence interval from -0.363 to 0.454 and an unadjusted p-value of 0.827.

Those data do not establish a clear difference between the conditioning strategies. They also do not establish that the strategies are equivalent. The primary interval is broad, the arm sizes are limited, and the outcome count is not accompanied by a full definition or time-to-event analysis. The registry note about 2 patients in the nonmyeloablative arm who did not receive transplant adds an analysis-population question that the record does not resolve.

The secondary outcomes provide context about transplantation and disease-related events but do not deliver a consistent pattern that settles the primary comparison. Their interpretation is further limited because the registry record does not report analyses for them or a multiplicity plan. Adverse event counts are descriptive and likewise do not establish comparative safety.

As a general statistical principle, absence of strong evidence for a difference is not proof that there is no difference. A small and imprecise trial may leave substantial uncertainty even when a point estimate is near zero or an unadjusted p-value is not small. The posted results should therefore be understood as limited evidence from this trial, not as a definitive answer about the comparative effects of the regimens in all patients with the listed conditions.

The results do not support medical advice for an individual patient. Treatment choices require clinical judgment and information beyond the registry results, including patient circumstances and evidence not described in this record.

17. Why This Trial Matters Statistically

This trial is statistically notable because it compares two conditioning intensities in a randomized phase III design and reports an outcome intended to capture survival. Randomization is an important design feature for comparative inference: in general, it aims to balance measured and unmeasured prognostic factors across groups at assignment. The trial’s results therefore address a meaningful comparative question, even though the record’s analysis details are incomplete.

The case also illustrates why design labels do not guarantee precise estimates. The registry lists an enrollment of 25, while the posted primary outcome denominators are 12 and 11. The primary risk-difference interval extends from -0.363 to 0.454. This breadth makes clear that the observed estimate alone cannot determine the magnitude or direction of the underlying difference with confidence.

Another statistical lesson is the distinction between a survival endpoint and a count recorded at a follow-up point. Overall survival is commonly analyzed using time-to-event methods when follow-up times and censoring differ, but the registry posts participant counts and does not describe a survival curve or time-to-event model. That does not demonstrate that no such analysis occurred; it means the registry record does not report one.

The record also brings attention to analysis population and multiplicity. It notes that 2 patients in the nonmyeloablative arm did not receive transplant, yet does not explain how those patients were handled for the primary outcome. Several secondary outcomes are listed, but no analysis plan or multiplicity approach is reported. These details are essential for understanding exactly what a comparison estimates and how much weight to place on secondary findings.

Together, these features make the trial a useful example of interpreting randomized evidence with limited precision and incomplete statistical reporting. The appropriate conclusion is calibrated: the posted comparison is informative about the observed data, but it leaves substantial uncertainty about the comparative effect.

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.

The primary outcome is labeled overall survival at 2 years, but the registry reports it as a participant count and does not define the count in further detail. It does not post a time-to-event estimate, survival curve, hazard ratio, or censoring method. This limits direct interpretation of the result as a survival analysis.

The registry notes that 2 patients in the nonmyeloablative arm did not receive transplant because of relapse and withdrawal of consent, but does not state how they were handled in the primary analysis. The analysis population, follow-up after nonreceipt of transplant, and missing-data procedures are not reported in the registry record.

The posted primary arm denominators are 12 and 11, and the confidence interval is wide. The result is therefore imprecise. The registry record does not report the trial’s original sample-size justification, the intended statistical test, or a precision target. Planning illustrations based on the observed effect should not be mistaken for the original design rationale.

The myeloablative arm includes two treatment groups in the regimen description, but the descriptions are incomplete. The registry also does not provide baseline characteristics that would help readers assess the composition of the analyzed groups. Details on allocation concealment, outcome assessment procedures, protocol deviations, and follow-up completeness are not reported in the registry record.

Finally, several secondary outcomes are listed, but the registry does not report analyses for them or a multiplicity strategy. Adverse-event counts and terms lack context on exposure time, detailed definitions, and arm-specific attribution for the listed serious terms. These limitations constrain the conclusions that can be drawn from the posted record without implying that unreported procedures were not conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Low-Dose or High-Dose Conditioning Followed by Peripheral Blood Stem Cell Transplant in Treating Patients With Myelodysplastic Syndrome or Acute Myelogenous Leukemia — NCT00322101.
• Registry record last updated 2014-10-31; status last verified 2014-10.
• Results first posted 2013-10-28.
• 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 describes a completed randomized, parallel-group, unmasked phase III trial sponsored by Fred Hutchinson Cancer Center. It compared nonmyeloablative with myeloablative conditioning followed by allogeneic peripheral blood stem cell transplantation in patients with myelodysplastic syndromes or acute myeloid leukemia. The listed enrollment is 25; the primary outcome is overall survival at 2 years.

The registry posts primary counts of 6 of 12 in the nonmyeloablative arm and 6 of 11 in the myeloablative arm. The unadjusted risk difference is 0.045, with a 95% confidence interval from -0.363 to 0.454 and p = 0.827. The estimate is imprecise and does not establish a clear difference or equivalence.

Several secondary outcomes and adverse-event counts are also listed, but the registry record does not report the full analysis plan, multiplicity handling, or details of the primary analysis population. It notes that 2 patients in the nonmyeloablative arm did not receive transplant, without explaining how they were handled in the primary analysis.