Chemotherapy in Treating Patients With Myelodysplastic Syndrome Before Donor Stem Cell Transplant: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Chemotherapy in Treating Patients With Myelodysplastic Syndrome Before Donor Stem Cell Transplant (NCT01812252), a randomized phase 2 study. The primary outcome is Failure-free Survival (Failure Defined as Death or Relapse).

2. Clinical Question

The trial asks whether outcomes differ between two approaches to initial cytoreductive chemotherapy before allogeneic hematopoietic cell transplantation for people with myelodysplastic syndrome. The primary endpoint is failure-free survival at 18 months, with failure defined as death or relapse. The registry records 6 participants with an endpoint event in Arm A and 10 in Arm B, with 25 participants in each arm.

The comparison is between a treatment approach based on decitabine or azacitidine and a physician-choice induction-like chemotherapy regimen. The trial is randomized, but the registry record does not report the allocation procedure in enough detail to describe how the random sequence was generated or concealed. It also does not report the original statistical plan, so the endpoint counts and posted unadjusted comparison should be read as the recorded results rather than as a complete account of the trial’s analysis.

3. Trial Design

The ICT-HCT study is a phase 2 randomized, parallel-arm trial with no masking. The registry lists an enrollment of 50 participants and 25 participants in each arm for the primary outcome. The sponsor is Fred Hutchinson Cancer Center. The record lists the study as completed, with a start date of 2013-08-19 and a primary completion date of 2022-10-26.

Arm A received decitabine or azacitidine. The arm description says treatment was given intravenously or subcutaneously per standard of care and repeated per standard of care, for 4 cycles of decitabine or 6 cycles of azacitidine, unless disease progression or unacceptable toxicity occurred. Arm B received a physician-selected standard-of-care or other experimental protocol using induction-like chemotherapy. The registry explicitly notes that no single regimen was required and that listed regimens were examples only. Thus, Arm B represents a treatment strategy with more than one possible regimen, rather than one uniform drug regimen.

Quality-of-life assessment was also listed as an intervention. Secondary outcomes included quality-of-life measures using the EORTC QLQ-C30 and EORTC QLQ-HDC29 questionnaires, overall survival, post-transplant relapse counts, and the number of participants receiving hematopoietic cell transplantation. The registry lists five secondary outcomes as posted. Their numerical results are not reported in the registry record used for this analysis.

The registry record does not report the randomization sequence method, allocation concealment, detailed eligibility criteria, or the planned statistical analysis. It also does not report why the study enrolled 50 participants or how that enrollment target was chosen. These omissions limit how fully the design can be assessed from the posted record alone.

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.

Before assignment: This study is a multi-center, open-label randomized study of intensive chemotherapy versus hypomethylating agent-based therapy as the initial pre-transplant cytoreductive therapy in patients with myelodysplastic syndrome. Patients will be randomized to receive treatment with either hypomethylating agent therapy or intensive chemotherapy; they will not receive both.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Number of subjects enrolled and randomized in each arm.

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: Eligible patients will be randomized in a 1:1 fashion. The primary outcome will be analyzed on an intention-to-treat basis.

6. Primary Endpoint

The registry lists the primary outcome as Failure-free Survival (Failure Defined as Death or Relapse), measured over 18 months.

The primary endpoint is titled failure-free survival, with failure defined as death or relapse, and its timeframe is 18 months. In this context, a participant who dies or experiences relapse meets the stated definition of failure. The registry’s outcome entries are counts of participants, rather than a posted survival curve or a time-to-event estimate. It records 6 participants in Arm A and 10 in Arm B for the endpoint.

Failure-free survival is used to combine two clinically important events into one endpoint: death and relapse. Combining events can give a broader picture of time without either event than assessing relapse alone. It also means the combined result does not reveal how many failures arose from each component. Component-specific counts and the timing of events are not reported in the registry record.

The endpoint title and timeframe should not be confused with a full time-to-event analysis. The posted outcome is presented as counts among participants enrolled and randomized in each arm. The record does not show individual event times, censoring information, or an estimate of the probability of remaining failure-free through 18 months. The counts therefore describe the posted endpoint entries but do not, on their own, provide a complete account of the survival experience over time.

7. Results Posted in the Registry

• Arm B (Induction-like Chemotherapy Regimen): 40.0% (10/25) versus 24.0% (6/25) on control; risk difference 16.0 percentage points (95% CI -9.5 to 41.5), risk ratio 1.67 (0.71–3.89); unadjusted two-proportion z-test p = 0.225.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry reports a binary participant-count outcome for the primary endpoint. Each participant is represented as having or not having the defined endpoint event in the posted count. General statistical explanation: for a binary endpoint, an arm-level event proportion can be compared between arms, but a count alone does not convey event timing. Although the endpoint is called failure-free survival, the posted results do not include individual follow-up times or censoring data.

What does the risk difference describe?

The posted risk difference is 0.16 for Arm B relative to Arm A. A risk difference compares the event proportions between two groups by subtraction, with the sign depending on the stated arm order. A positive value in this comparison indicates a higher observed event proportion in Arm B than in Arm A. It is an absolute contrast, not a relative change. The registry also reports a confidence interval for this difference; because the interval spans values on both sides of no difference, the data are compatible with a range of possible contrasts, including no difference.

General explanation: an unadjusted risk difference uses the observed arm summaries without accounting for other participant characteristics or covariates. It can be easy to interpret as an absolute group contrast, but it does not address imbalances that may occur by chance in a small trial. The record does not report an adjusted model or covariate analysis, so no adjusted effect estimate can be described.

How should the p-value be read?

The registry lists an unadjusted p-value of 0.225. General explanation: a p-value measures how unusual results at least as discrepant as the observed result would be under a specified null hypothesis and the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. A p-value also does not quantify the size or practical importance of the difference. The registry record does not identify the test details or say whether this p-value was adjusted for multiple comparisons.

The endpoint counts are small, so the observed arm summaries can be sensitive to a small number of participants. General explanation: with limited data, uncertainty in estimated event proportions and their difference is often substantial. Confidence intervals communicate a range of values compatible with the data and model assumptions, rather than giving a guarantee that the true value lies in that range. Interpretation also depends on whether the endpoint definition, follow-up, and analysis population were applied consistently across arms; details of these procedures are not reported in the registry record.

Why does the endpoint label need context?

Failure-free survival is ordinarily understood as an endpoint involving time until a defined event, but the record presents participant counts and labels the measure as a count of participants. General explanation: time-to-event analyses use information about when events occur and can account for participants who have not experienced an event by the end of their observed follow-up. A simple count does not show those event times, how long each participant was followed, or how incomplete follow-up was handled. The posted data therefore do not support reconstruction of a survival curve or a time-to-event hazard comparison.

The registry specifies death or relapse as failure, but it does not provide separate counts for those components. This prevents assessment of whether one component accounts for most of the combined endpoint. The record also does not state how a participant with incomplete follow-up was classified, whether there were competing events, or whether any endpoint adjudication procedure was used. These are relevant details for interpreting a time-to-event endpoint, and they are not reported in the registry record.

What can be learned from the sample-size illustration?

The planning illustration uses the observed effect and states assumptions of a two-sided significance level of 0.05, equal allocation, and a normal approximation. Its rows consider planning for 100%, 75%, and 50% of the observed effect. The figures are participants per arm for this binary endpoint, not total event counts. General explanation: the smaller the effect one aims to detect, the more participants are generally needed, because a smaller difference is harder to distinguish from random variation. The illustration is not the trial’s original sample-size justification, and the original design assumptions are not reported in the registry record.

The registry lists no posted analyses beyond the comparison summarized for the primary endpoint. It does not report a statistical analysis plan, the handling of missing data, adjustment for multiplicity, interim monitoring, or an analysis population definition. General statistical principles can explain why those details matter, but they cannot fill in what the trial team actually planned or did. Accordingly, the methods interpretation should remain bounded by the posted counts and unadjusted comparison.

10. Confidence Intervals and Precision

The registry reports a confidence interval for the risk difference between Arm B and Arm A. The interval includes both negative and positive values, so it includes no difference and also allows for differences in either direction. Its breadth indicates that the estimated contrast is not precise. The posted counts, 6 in Arm A and 10 in Arm B, come from 25 participants per arm, so the data offer limited precision for distinguishing the treatment approaches.

General explanation: a confidence interval expresses uncertainty around an estimate under the assumptions of the method used. It is not a range containing every plausible result, nor does it represent the probability that the particular interval contains the true effect. The confidence level and exact interval method are not stated in the registry record, so those features cannot be specified from the posted record. The interval is best read together with the observed risk difference and the event counts, rather than in isolation.

The unadjusted p-value is 0.225, but it does not replace the interval as a description of precision. A p-value gives a test-based summary relative to a null hypothesis; the interval conveys the range of effect estimates compatible with the observed data and its method. Since the interval extends across no difference, the observed contrast does not pinpoint a clear direction or magnitude. The small number of participants and events also means modest changes in the observed counts could materially alter the estimated contrast.

The registry does not provide event-time information, follow-up completeness, or censoring details. Consequently, precision cannot be assessed for a time-to-event estimate from the posted counts. The reported interval pertains to the posted risk-difference comparison, not to a reconstructed survival analysis.

11. Planning a Similar Trial: Sample Size

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

The planning figures are stated as participants per arm for this binary participant-count outcome. They are not total event counts. The illustration assumes a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. Its rows show planning for 100%, 75%, and 50% of the observed effect. The corresponding values are 133 and 177 participants per arm for 80% and 90% power when planning for 100% of the observed effect; 228 and 305 for 75%; and 494 and 660 for 50%.

In plain language, the 80% power column gives the estimated number of participants per arm under which the stated assumptions would give an 80% chance of detecting the specified effect if that effect were the true one. The 90% column expresses the same idea with a higher target chance of detecting it. These are planning quantities, not results from participants enrolled in this trial. The illustration is not observed power.

The rows use fractions of the observed effect as planning targets. A smaller target effect requires more participants because a smaller between-arm difference is harder to distinguish from chance variation. The figures are based on the observed result, so they should not be treated as a recommendation or as evidence that the original trial was designed to detect that effect. The original sample-size justification and the trial’s own design assumptions are not reported in the registry record.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.240; treatment proportion p₁ = 0.400; average p̄ = 0.320.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6597 = 1.2930.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6499 = 0.5470.
4. n = (1.2930 + 0.5470)² / (0.1600)² = 132.2, rounded up to 133 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 <- 0.24                          # control proportion
p1 <- 0.4                          # 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(1812252)
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 = 133 (80% power), 177 (90% power)
 75% of observed effect: n per arm = 228 (80% power), 305 (90% power)
 50% of observed effect: n per arm = 494 (80% power), 660 (90% power)
power.prop.test: 132.2 
Simulated power at n = 133 per arm: 0.813 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, including two quality-of-life questionnaires, overall survival, post-transplant relapse counts, and receipt of hematopoietic cell transplantation. Multiple outcomes create the possibility of multiple statistical comparisons. General explanation: when many hypotheses are tested, the chance of at least one apparently notable result can increase unless the analysis plan accounts for multiplicity. The registry record does not report whether any correction, hierarchy, or other multiplicity strategy was planned or applied.

The posted results include the primary endpoint counts and an unadjusted comparison, but no posted analyses are listed for the secondary outcomes. Their numerical findings, analysis methods, and missingness are not reported in the registry record. The record also does not report whether any interim analyses were planned or conducted, or whether stopping rules were used.

Missing-data methods and analysis populations are also not described. The registry says the primary endpoint population is the number of subjects enrolled and randomized in each arm, but does not explain how participants with incomplete follow-up, withdrawal, or unavailable outcome information were handled. It does not state whether the analysis followed assigned treatment regardless of treatment received, whether a per-protocol analysis was conducted, or how protocol deviations were treated.

These gaps matter because analysis choices can affect which participants contribute to an estimate and how uncertainty is calculated. General explanation: intention-to-treat and per-protocol analyses answer different questions, while methods for incomplete follow-up can influence endpoint estimates. Those concepts do not establish which approach was used in this trial. The posted record does not support claims about the trial’s multiplicity control, missing-data assumptions, or analysis populations beyond the stated enrolled-and-randomized population description.

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

The posted results describe an observed difference in the number of primary endpoint events: 6 participants in Arm A and 10 in Arm B, with 25 participants in each arm. The risk difference is 0.16 for Arm B relative to Arm A, and the unadjusted p-value is 0.225. The confidence interval includes no difference and values in either direction. Together, these summaries show that the direction and size of the underlying difference are uncertain.

These results do not establish that one chemotherapy strategy is superior, equivalent, or inferior. A failure to demonstrate a clear difference is not proof that the approaches have identical effects. Conversely, the observed difference in counts is not by itself evidence of a causal effect. Randomization supports a comparative design, but interpretation still depends on implementation, follow-up, outcome ascertainment, and analysis details that are not fully reported in the registry record.

The comparison also concerns treatment strategies as recorded, not necessarily single standardized regimens. Arm A allowed decitabine or azacitidine, while Arm B permitted a physician-selected induction-like regimen and did not require one specific regimen. The registry does not report how often each regimen was used, treatment exposure, or treatment changes. The result therefore cannot identify the effect of a particular drug or regimen within either arm.

The endpoint combines death and relapse, and the record does not separate those components. The posted counts also do not show when events happened or how follow-up was handled. Thus, they cannot answer questions about the timing of failure, the shape of failure-free survival over time, or the separate contributions of death and relapse. The secondary outcomes are listed, but their results are not reported in the registry record.

General explanation: clinical interpretation ordinarily considers the estimated effect, its uncertainty, outcome relevance, and the design and analysis methods together. In this trial, the summary supports a description of the observed counts and their imprecision, but the incomplete reporting limits broader interpretation. The results should not be used alone to make treatment decisions.

15. Why This Trial Matters Statistically

This trial is statistically interesting because it compares treatment approaches before transplantation while using a combined endpoint that includes both death and relapse. That endpoint can summarize more than one type of failure, but its interpretation depends on understanding the component events and their timing. The registry reports neither component-specific counts nor event-time data, illustrating why endpoint labels and posted outcome formats need to be read together.

The randomized parallel-arm design provides a framework for comparing strategies, but the actual strategies differ in how tightly they are specified. Decitabine or azacitidine were used in Arm A, while Arm B allowed physician choice among induction-like regimens. This flexibility may reflect a comparison of clinical approaches, yet it makes the result less specific to any one regimen. The registry does not provide the treatment distribution needed to examine that heterogeneity.

The small enrolled population and the broad interval around the risk difference highlight the role of precision in interpreting randomized trials. The observed counts alone may look different across arms, while the uncertainty leaves multiple underlying differences compatible with the data. The result is a useful example of why a point estimate, interval, and test result should be considered together rather than reducing interpretation to a single threshold.

Finally, the registry record distinguishes a planning illustration based on the observed effect from the trial’s original design rationale. It reports the former assumptions and figures, but not the original sample-size justification or full analysis plan. That distinction is important when statistical planning information is used to understand what a completed trial can and cannot establish.

16. 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 main limitation of the posted primary result is that it is presented as participant counts rather than a detailed time-to-event analysis, despite the failure-free survival endpoint label. The registry does not report event times, censoring, follow-up completeness, or separate counts for death and relapse. The counts therefore cannot describe the course of failure-free survival over the 18-month timeframe in detail.

The primary comparison involves 25 participants per arm, and its confidence interval includes no difference and values in both directions. This limits precision. The registry record does not report the original sample-size justification, so it is not possible to determine from the record what effect the trial was intended to detect or how the enrollment target was selected.

Treatment heterogeneity is another limitation for regimen-specific interpretation. Arm A could receive decitabine or azacitidine, and Arm B allowed physician choice among induction-like regimens. The record does not state how many participants received each regimen or whether treatments changed. It therefore does not support isolating effects of individual regimens.

Important methodological details are also absent. Randomization implementation, allocation concealment, missing-data handling, analysis populations, multiplicity procedures, and interim analyses are not reported in the registry record. The secondary outcomes are listed but their numerical results are not reported. The adverse-event fields list zero participants at risk alongside zero affected, and the record does not explain those entries; they cannot be interpreted as a complete adverse-event assessment. These limitations constrain conclusions to the posted counts and unadjusted comparison.

17. Related Tutorials

18. Related Statistical Calculators

19. Sources

• ClinicalTrials.gov: Chemotherapy in Treating Patients With Myelodysplastic Syndrome Before Donor Stem Cell Transplant — NCT01812252.
• Registry record last updated 2024-02-15; status last verified 2024-01.
• Results first posted 2024-02-15.
• 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.

20. Record Summary

The registry record describes NCT01812252, the phase 2 randomized ICT-HCT study of initial cytoreductive therapy before allogeneic hematopoietic cell transplantation. It lists a completed, unmasked, parallel-arm trial sponsored by Fred Hutchinson Cancer Center, with enrollment of 50 participants.

The primary endpoint is 18-month failure-free survival, with failure defined as death or relapse. The registry records 6 endpoint events among 25 participants in the decitabine-or-azacitidine arm and 10 among 25 participants in the induction-like chemotherapy arm. The posted risk difference is 0.16, with an unadjusted p-value of 0.225 and a confidence interval spanning no difference.

The record lists quality-of-life and other secondary outcomes but does not report their numerical results. It also does not report the original sample-size justification, detailed statistical plan, missing-data procedures, or analysis-population methods. The primary comparison is therefore best understood as an uncertain summary of the posted endpoint counts, not a complete account of the trial’s analyses.