Tacrolimus and Mycophenolate Mofetil With or Without Sirolimus in Preventing Acute Graft-Versus-Host Disease in Patients Who Are Undergoing Donor Stem Cell Transplant for Hematologic Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tacrolimus and Mycophenolate Mofetil With or Without Sirolimus in Preventing Acute Graft-Versus-Host Disease in Patients Who Are Undergoing Donor Stem Cell Transplant for Hematologic Cancer (NCT00105001), a randomized phase 2 study. The primary outcome is Number of Participants With Grades II-IV Acute GVHD.

2. Clinical Question

The clinical question concerns prevention of acute GVHD after donor stem cell transplantation. The registry describes the biologic context: donor immune cells can react against the recipient’s normal tissues, while donor stem cells may also replace the recipient’s immune system and contribute to a graft-versus-tumor effect. The trial therefore studied post-transplant immunosuppression schedules in a setting where the outcome of interest was acute GVHD, rather than a general measure of transplant success.

The primary endpoint was the number of participants with grades II–IV acute GVHD by 150 days after transplant. The posted counts were 44.0 of 69.0 in Arm I, 34.0 of 71.0 in Arm II, and 32.0 of 68.0 in Arm III. These are observed event counts, not estimates of treatment effect adjusted for other characteristics. The registry record does not report a more detailed primary clinical question or a formal hypothesis statement.

3. Trial Design

This was a randomized, open-label, parallel-group phase II trial. The registry lists an enrollment of 210. Its stated purpose was to determine the most promising postgrafting immunosuppression strategy for prevention of acute GVHD after unrelated-donor G-CSF-mobilized peripheral blood mononuclear cell transplantation using nonmyeloablative conditioning. The sponsor was Fred Hutchinson Cancer Center. The registry lists the trial as completed.

Three arms were reported. Arm I used MMF and tacrolimus: tacrolimus was scheduled every 12 hours from days -3 to 180, with taper beginning on day 100 in the absence of GVHD. MMF was scheduled every 8 hours on days 0-29 and every 12 hours on days 30-96, with taper beginning on day 40 in the absence of GVHD. Arm II also used MMF and tacrolimus, but on an alternate schedule: tacrolimus was scheduled from days -3 to 150, and MMF from days 0-29 every 8 hours and days 30-180 every 12 hours; the described taper timing was day 100 for tacrolimus and day 150 for MMF in the absence of GVHD. Arm III used the Arm II schedules and added sirolimus once daily on days -3 to 80.

The registry describes fludarabine phosphate and total-body irradiation as conditioning interventions, alongside peripheral blood stem cell and allogeneic hematopoietic stem cell transplantation. The primary endpoint was assessed 150 days after transplant. Two subjects counted toward accrual did not proceed to transplant and were not evaluable for that endpoint. The registry record does not report the randomization procedure, allocation concealment, the original sample-size justification, or more detailed eligibility criteria beyond the listed conditions and transplant context.

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: Two subjects counted towards accrual but did not proceed to transplant and thus were not evaluable.

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 Number of Participants With Grades II-IV Acute GVHD, measured over 150 days after transplant.

The primary endpoint counted participants who developed grades II–IV acute GVHD by 150 days after transplant. The registry describes acute GVHD grading using skin, liver, and gut involvement. Skin and liver findings are assigned stages, and gut severity is based on the most severe involvement noted. The listed grade definitions identify grade II with stage 1–2 skin involvement and no gut or liver involvement, grade III with stage 2–4 gut and/or liver involvement, and grade IV with a severe pattern or death.

This endpoint is clinically relevant to a trial of post-transplant immunosuppression because the stated aim was prevention of acute GVHD. Combining grades II–IV makes the outcome a count of participants crossing the registry’s stated threshold, rather than a measure of the number or duration of episodes, time to onset, or severity within each grade. The endpoint was binary at the participant level: each participant either was or was not counted as having the specified grades during the stated follow-up period.

The posted counts were 44.0 participants in Arm I, 34.0 in Arm II, and 32.0 in Arm III. The corresponding arm sizes were 69.0, 71.0, and 68.0. The registry notes that two subjects counted toward accrual did not proceed to transplant and were not evaluable. It does not report further detail on endpoint adjudication, handling of incomplete follow-up, or whether GVHD events after the stated assessment window were included.

7. Results Posted in the Registry

• Arm II (MMF and Tacrolimus Alternate Schedule): 47.9% (34/71) versus 63.8% (44/69) on control; risk difference -15.9 percentage points (95% CI -32.1 to 0.4), risk ratio 0.75 (0.56–1.01); unadjusted two-proportion z-test p = 0.059.
• Arm III (MMF, Tacrolimus, and Sirolimus): 47.1% (32/68) versus 63.8% (44/69) on control; risk difference -16.7 percentage points (95% CI -33.1 to -0.3), risk ratio 0.74 (0.54–1.00); unadjusted two-proportion z-test p = 0.049.

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.

Number of Non-Relapse Mortalities

• 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 (MMF and Tacrolimus Alternate Schedule): 8.5% (6/71) versus 4.3% (3/69) on control; risk difference 4.1 percentage points (95% CI -4.0 to 12.2), risk ratio 1.94 (0.51–7.47); unadjusted two-proportion z-test p = 0.322.
  • Arm III (MMF, Tacrolimus, and Sirolimus): 2.9% (2/68) versus 4.3% (3/69) on control; risk difference -1.4 percentage points (95% CI -7.7 to 4.9), risk ratio 0.68 (0.12–3.92); unadjusted two-proportion z-test p = 0.661.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (MMF and Tacrolimus Alternate Schedule) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm III (MMF, Tacrolimus, and Sirolimus) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Utilizing High-Dose Corticosteroids

• 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 (MMF and Tacrolimus Alternate Schedule): 49.3% (35/71) versus 55.1% (38/69) on control; risk difference -5.8 percentage points (95% CI -22.3 to 10.7), risk ratio 0.90 (0.65–1.23); unadjusted two-proportion z-test p = 0.494.
  • Arm III (MMF, Tacrolimus, and Sirolimus): 32.4% (22/68) versus 55.1% (38/69) on control; risk difference -22.7 percentage points (95% CI -38.9 to -6.6), risk ratio 0.59 (0.39–0.88); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (MMF and Tacrolimus Alternate Schedule) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm III (MMF, Tacrolimus, and Sirolimus) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Surviving Overall

• 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 (MMF and Tacrolimus Alternate Schedule): 66.2% (47/71) versus 69.6% (48/69) on control; risk difference -3.4 percentage points (95% CI -18.8 to 12.1), risk ratio 0.95 (0.76–1.20); unadjusted two-proportion z-test p = 0.670.
  • Arm III (MMF, Tacrolimus, and Sirolimus): 58.8% (40/68) versus 69.6% (48/69) on control; risk difference -10.7 percentage points (95% CI -26.7 to 5.2), risk ratio 0.85 (0.66–1.09); unadjusted two-proportion z-test p = 0.190.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (MMF and Tacrolimus Alternate Schedule) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm III (MMF, Tacrolimus, and Sirolimus) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address several distinct aspects of the transplant course: non-relapse mortality by 200 days, high-dose corticosteroid use by 150 days, overall survival at 1 year post-transplant, and survival without progression. Across these outcomes, the observed counts and re-calculated contrasts do not form one uniform pattern. The registry’s sponsor-reported analyses also vary by endpoint, with some outcomes having an overall three-group analysis and only selected pairwise results reported.

These secondary outcomes complement the primary endpoint by describing mortality, treatment use, and later survival-related status. They do not directly measure the same event as grades II–IV acute GVHD, and they cannot by themselves establish why an outcome differed or whether it is related to GVHD. They should be interpreted as separate results with their own follow-up periods and definitions.

Unadjusted secondary findings carry less weight when many outcomes and comparisons are examined without a stated multiplicity plan. In general, testing a larger family of hypotheses increases the chance that at least one result will appear noteworthy by chance. The registry record does not report whether secondary endpoints were ordered by priority, whether formal adjustment was planned, or whether these analyses were intended as confirmatory. Consequently, an isolated unadjusted result should be treated cautiously and considered alongside the full pattern of outcomes, their uncertainty, and the primary analysis.

Survival outcomes also require care in interpretation. A participant count at a specified time is not the same as a full time-to-event analysis, and the record does not provide enough detail to determine how censoring or follow-up completeness was handled in each reported analysis. The overall secondary pattern offers context, but the registry record does not establish a single consistent advantage across these different endpoint domains.

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

• Number of Non-Relapse Mortalities
• Number of Participants Utilizing High-Dose Corticosteroids
• Number of Participants Surviving Overall
• Number of Participants Surviving Without Progression

9. Statistical Interpretation

10. Statistical Methods Explained

General: The primary endpoint is a binary participant-level outcome: a participant is counted as having grades II–IV acute GVHD or not. For this kind of outcome, an arm’s event count is interpreted alongside the number of participants assessed. The posted counts are 44.0 of 69.0 for Arm I, 34.0 of 71.0 for Arm II, and 32.0 of 68.0 for Arm III. Counts are straightforward to understand, but a count alone does not describe the size or uncertainty of a between-arm contrast.

The re-calculated comparisons use the risk difference, which expresses the contrast between the event risks in two arms. A negative value in these comparisons means the observed risk was lower in the named comparison arm than in Arm I. For the primary endpoint, the re-calculated risk difference was -0.159 for Arm II versus Arm I and -0.167 for Arm III versus Arm I. These simple unadjusted calculations use posted summary counts and do not account for additional participant-level information or covariates. They should not be confused with adjusted or time-to-event analyses.

General: A confidence interval describes a range of values compatible with the data and the calculation method, under its assumptions. It communicates precision as well as the direction of an estimate. A narrow interval indicates greater precision than a wide interval, but even a narrow interval does not remove limitations in study conduct or analysis. For the primary risk differences, the 95% intervals were -0.321 to 0.004 for Arm II and -0.331 to -0.003 for Arm III. The first interval crosses zero; the second narrowly does not. The point estimates should therefore be read together with the ranges, rather than in isolation.

General: A p-value measures how compatible the observed data are with a specified null hypothesis under a particular statistical model. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. The unadjusted p-values for the primary re-calculations were 0.059 for Arm II and 0.049 for Arm III. The registry’s sponsor-reported primary analyses use a Cox regression label and report a three-group p-value of 0.09, along with pairwise hazard ratios. The registry record does not explain the model specification, covariates, event-time definition, or the basis for the difference between those analyses and the unadjusted re-calculations.

The sponsor-reported analysis should not be conflated with the simple risk-difference calculations. A Cox regression analysis is a time-to-event approach and reports a hazard ratio, whereas the re-calculations compare the observed proportions at a stated follow-up time. These answer related but not identical statistical questions. The registry record labels the reported analyses as “Regression, Cox,” but does not give enough detail to reconstruct them or determine why the estimates differ from the posted summary-count calculations. Because a discrepancy is flagged, the sponsor’s own analysis takes precedence for the trial’s reported inferential result.

General: Random allocation can help balance known and unknown characteristics across treatment arms, on average, but it does not guarantee that groups are identical in a particular trial. The registry identifies the study as randomized, but its record does not report the sequence-generation method, concealment procedures, stratification factors, or baseline characteristics in the information summarized for these results. The open-label designation means masking was absent. The record does not state whether outcome assessors were masked.

General: Multiple comparisons matter when more than one treatment contrast, endpoint, or analysis is examined. Each additional test gives another opportunity for a result to appear notable by chance if the underlying effects are absent. An unadjusted p-value evaluates an individual comparison without accounting for the family of analyses. The record lists three arms, multiple sponsor analyses, and secondary outcomes, but it does not report a multiplicity strategy. Thus, the re-calculated p-values should be read as unadjusted, exploratory comparisons rather than as a complete multiplicity-controlled testing framework.

The registry reports counts at specified follow-up times for the primary and secondary outcomes. A time-to-event model can account for when events occur and can handle censoring under its assumptions, while a fixed-time binary count summarizes whether an event was observed by the stated time. The registry record does not report the censoring details or assumptions used in the sponsor’s Cox analyses. General statistical interpretation therefore requires distinguishing the posted fixed-time counts from the sponsor’s reported regression results, rather than treating them as interchangeable estimates.

For binary outcomes, sparse event counts can make estimates imprecise, particularly when few participants experience the event. The non-relapse mortality comparisons illustrate this issue: the arm counts were 3.0, 6.0, and 2.0, and the re-calculated confidence intervals were broad. General caution is warranted in interpreting rare-event contrasts because a small change in observed counts can correspond to substantial uncertainty. The record does not report whether a specific sparse-data method was used in the sponsor analysis.

11. Confidence Intervals and Precision

The precision of the primary re-calculated comparisons is reflected by their 95% confidence intervals. For Arm II versus Arm I, the risk difference was -0.159, with an interval from -0.321 to 0.004. For Arm III versus Arm I, it was -0.167, with an interval from -0.331 to -0.003. The intervals are wide relative to their point estimates, indicating that the summaries are compatible with a range of possible contrasts. The Arm II interval includes zero, while the Arm III interval ends just below zero.

These intervals describe uncertainty under the unadjusted calculation based on the posted arm counts. They do not incorporate any adjustment from the sponsor’s regression analyses, and they do not account for potential missing outcomes or other design features not described in the registry record. They also should not be interpreted as a range containing a known true effect with certainty. In general, a confidence interval is a measure of sampling uncertainty under a specified method, not a guarantee about the clinical effect.

The sponsor’s pairwise primary analyses report hazard ratios rather than risk differences. For Arm II versus Arm I, the reported hazard ratio was 0.69 with a 95% confidence interval of 0.4 to 1.1. For Arm III versus Arm I, it was 0.62 with a 95% confidence interval of 0.6 to 1.0. Those results reflect the registry’s reported Cox regression analyses and should be interpreted separately from the fixed-time risk-difference intervals. The registry record does not provide enough model detail to explain the differences between these measures or reproduce the sponsor’s calculations.

Confidence intervals for the secondary re-calculations also vary in width. In particular, the non-relapse mortality contrasts have broad intervals, consistent with limited precision for outcomes with few observed events. The record’s counts and intervals are more informative than a p-value alone, but they do not remove the uncertainty associated with the trial’s size, event numbers, and incompletely reported analysis details.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design. All figures in this sample-size material are participants per arm, rather than total participants or total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm required, under those assumptions, for an 80% chance of detecting the chosen effect if that effect were the true one. The 90% column gives the corresponding per-arm planning figure for a 90% chance. Higher target power generally requires more participants for the same assumed effect. The rows for planning at 100%, 75%, and 50% of the observed effect show how the required sample changes when the planning target is smaller. Smaller effects need more participants to detect reliably.

For example, for the primary comparison of Arm II with Arm I, the illustration lists 153 participants per arm for 80% power when planning for 100% of the observed effect, 269 for 75%, and 598 for 50%. The corresponding figures for Arm III versus Arm I are 138, 244, and 541 participants per arm. These numbers are not observed outcomes and do not describe the probability that this completed trial detected an effect. This is not observed power.

The registry record does not report the trial’s own original sample-size justification or planning assumptions. The illustration is a separate calculation using the stated assumptions and observed summary effect; it should not be read as evidence that the trial was designed around those figures.

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 = 0.638; treatment proportion p₁ = 0.479; average p̄ = 0.558.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7023 = 1.3765.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6933 = 0.5835.
4. n = (1.3765 + 0.5835)² / (-0.1588)² = 152.3, rounded up to 153 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 <- 0.63768115942029                          # control proportion
p1 <- 0.47887323943662                          # 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(105001)
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 = 153 (80% power), 204 (90% power)
 75% of observed effect: n per arm = 269 (80% power), 360 (90% power)
 50% of observed effect: n per arm = 598 (80% power), 800 (90% power)
power.prop.test: 152.3 
Simulated power at n = 153 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a three-group primary analysis labeled “Regression, Cox,” with p = 0.09. It also reports pairwise hazard ratios: 0.69 for Arm II versus Arm I, with a 95% confidence interval of 0.4 to 1.1 and p = 0.10; and 0.62 for Arm III versus Arm I, with a 95% confidence interval of 0.6 to 1.0 and p = 0.04.

The unadjusted re-calculations use the posted participant counts at 150 days and estimate risk differences. They give p-values of 0.059 for Arm II versus Arm I and 0.049 for Arm III versus Arm I. These are simple comparisons of the posted summaries and are not a reconstruction of the sponsor’s Cox regression. The two approaches use different effect measures and potentially different treatment of time and censoring.

A discrepancy is flagged between the sponsor analysis and the re-calculations. Accordingly, the sponsor’s own analysis takes precedence when describing the trial’s reported inferential findings. The registry record does not report sufficient model details, covariate adjustments, censoring information, or analysis-population details to reconcile the estimates. The re-calculations can provide a transparent descriptive comparison of the posted counts, but they should not replace the sponsor’s reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a three-arm trial, a primary endpoint, several secondary outcomes, and multiple reported analyses. It does not report a prespecified multiplicity strategy, such as a hierarchy among outcomes, a family of comparisons, or an adjustment to control the chance of false-positive findings across analyses. The primary re-calculated p-values and the secondary re-calculated p-values are therefore unadjusted. A borderline result in one comparison should not be interpreted as though it were the only test performed.

The record also does not report an interim-analysis plan, stopping rules, or whether any interim efficacy or safety analyses were conducted. These details should not be inferred from the completed status or from the results available in the registry. Likewise, the original statistical analysis plan and the trial’s own sample-size justification are not reported in the registry record.

For analysis populations and missing data, the primary endpoint description states that two subjects counted toward accrual but did not proceed to transplant and were not evaluable. The arm-level primary outcome counts are reported for the participants in the three arms, but the registry record summarized for these results does not fully describe the analysis population, handling of other missing outcomes, losses to follow-up, or use of an intention-to-treat approach. It does not state whether participants were analyzed according to assignment regardless of treatment received, nor how deviations from assigned schedules were handled.

These gaps matter because missingness and analysis-population choices can affect event counts and precision. The posted counts are useful descriptive information, but they do not reveal whether all randomized participants had complete endpoint ascertainment. Without the original analysis plan and fuller participant disposition, the extent to which the reported analyses followed prespecified methods cannot be assessed from the registry record alone.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: respiratory infection (4.2%), gvhd (2.9%), thrombosis (2.9%), sepsis (1.5%), gvhd w/ infection (1.5%).

The registry’s adverse-event summary reports serious adverse events and other adverse events by arm. For serious adverse events, the numbers at risk were 69 in Arm I, 71 in Arm II, and 68 in Arm III; the numbers affected were 9, 8, and 7, respectively. The summary lists 25, 22, and 25 participants affected by other adverse events in those arms. It also lists deaths of 21, 24, and 28 by arm. The registry record does not clarify in this summary how the death figures relate to specific adverse events or to the endpoint follow-up periods.

The listed serious adverse-event terms include respiratory infection (4.2%), GVHD (2.9%), thrombosis (2.9%), sepsis (1.5%), GvHD w/ infection (1.5%), and multi-organ failure (1.5%). The record does not specify in this summary whether these percentages use a pooled denominator, whether terms may overlap within participants, or the exact period of adverse-event collection.

These figures are descriptive counts, not adjusted comparisons of safety between arms. They do not establish that an event was caused by a particular schedule. Differences in counts should be interpreted with the arm sizes, follow-up, event definitions, and the record’s reporting limitations in mind.

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

The posted primary data show that fewer participants in Arm II and Arm III were counted as having grades II–IV acute GVHD by 150 days than in Arm I. The unadjusted comparison for Arm II has a confidence interval that includes zero, while the interval for Arm III narrowly excludes zero. The sponsor’s reported Cox analyses provide a different statistical analysis, and the flagged discrepancy means the sponsor analysis takes precedence for the trial’s own reported inference.

These results do not establish that any schedule works or does not work. They describe event counts and statistical contrasts in this trial, with uncertainty and limitations. The estimates are not a guarantee of the outcome for an individual participant, and they do not answer all relevant questions about risks and benefits. The registry record does not report enough methodological detail to resolve the difference between the sponsor analyses and the unadjusted re-calculations.

The trial’s three arms differed in the timing and duration of MMF and tacrolimus schedules, and Arm III added sirolimus to the Arm II schedule. Because the comparison is between complete schedules, the results cannot isolate the contribution of an individual drug or a particular dosing interval. The record also does not provide the detailed analysis plan or sufficient information on missing outcomes and participant disposition to determine how those issues affected the reported estimates.

The secondary endpoints address mortality, corticosteroid use, and survival-related outcomes, but they have different definitions and follow-up times. Their mixed pattern should be considered as context rather than as a single combined conclusion. In the absence of a reported multiplicity plan, secondary findings and individual unadjusted comparisons are less persuasive than results from a fully specified confirmatory analysis.

The statistical meaning is therefore limited to what the record documents: observed counts, selected sponsor analyses, and unadjusted re-calculations. The confidence intervals convey uncertainty but do not account for every source of uncertainty in the design or reporting. The information is not a substitute for the complete protocol, analysis plan, or full trial report, none of which is detailed in the registry record summarized for these results.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it compares three related immunosuppression schedules rather than a single intervention with a control. One arm changes the schedules of MMF and tacrolimus, while another adds sirolimus to that alternate schedule. This structure creates multiple clinically relevant contrasts, but it also makes it important to distinguish an overall three-group test from particular pairwise comparisons.

The primary endpoint is a participant count at a fixed follow-up time, while the sponsor reports Cox regression analyses and hazard ratios. Those are different representations of the outcome: one contrasts event proportions by the stated time, while the other is a time-to-event model. The difference between the sponsor’s reported results and the simple unadjusted re-calculations is a reminder that statistical conclusions depend on the estimand and analysis method, not just on the arm counts.

The primary re-calculations illustrate how uncertainty changes the interpretation of an apparent difference. Both point estimates are negative, but the Arm II interval crosses zero and the Arm III interval only narrowly excludes it. The sponsor’s own pairwise analyses report yet another set of estimates and p-values. Reporting counts, effect estimates, confidence intervals, and the sponsor’s analysis together is more informative than relying on a single threshold or p-value.

The registry also highlights issues common to clinical-trial interpretation: a broad disease population, incomplete reporting of analysis details, outcomes with different follow-up windows, and multiple comparisons. The two subjects not proceeding to transplant are explicitly identified as not evaluable for the primary endpoint, while other missing-data and analysis-population details are not reported. Such details matter for understanding which participants contribute to each result.

Finally, the planning illustrations connect observed effect size with future sample-size needs, while remaining distinct from the trial’s original design. They demonstrate that planning around smaller effects calls for more participants under the stated assumptions, but they do not show what the original investigators planned or what power this trial achieved.

19. 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.

Several limitations specific to this trial constrain interpretation. The study was open-label, with masking listed as none. The registry record does not state whether endpoint assessors were masked. Knowledge of assigned schedules could be relevant to treatment decisions and event assessment, although the available record does not describe whether or how this affected the endpoint.

The primary endpoint is a count of participants meeting a composite grade threshold by 150 days after transplant. That summary does not describe timing, duration, recurrence, or distribution of severity among participants who had GVHD. The registry supplies grading definitions but does not report additional information on adjudication or completeness of ascertainment.

The registry lists a broad range of hematologic conditions, while the primary outcome counts are pooled by arm. The record summarized for these results does not provide condition-specific outcome analyses or information about whether treatment effects differed across diagnoses. It is therefore not possible from these results alone to assess consistency across the listed conditions.

The trial includes three schedules and the posted re-calculations compare each non-control arm with Arm I. A discrepancy is flagged between the unadjusted summaries and sponsor analyses, and the record does not provide sufficient detail to reconcile them. The sponsor’s reported analysis takes precedence, but its model specification, covariates, censoring assumptions, and analysis population are not reported in the registry record.

Further limitations include unreported original sample-size assumptions, multiplicity procedures, interim analyses, and fuller details on missing outcomes and participant flow. Two subjects counted toward accrual did not proceed to transplant and were not evaluable for the primary endpoint; the record does not fully explain the handling of all other potential missing data. These omissions limit assessment of the prespecification and robustness of the reported results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Tacrolimus and Mycophenolate Mofetil With or Without Sirolimus in Preventing Acute Graft-Versus-Host Disease in Patients Who Are Undergoing Donor Stem Cell Transplant for Hematologic Cancer — NCT00105001.
• Registry record last updated 2019-10-30; status last verified 2019-10.
• Results first posted 2015-09-15.
• 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.

23. Record Summary

NCT00105001 is a completed randomized, open-label, parallel-group phase II trial sponsored by Fred Hutchinson Cancer Center. It compared three post-transplant immunosuppression schedules in patients undergoing unrelated-donor peripheral blood stem cell transplantation after nonmyeloablative conditioning. The registry lists an enrollment of 210.

The primary outcome was the number of participants with grades II–IV acute GVHD by 150 days after transplant. The posted counts were 44.0 of 69.0 in Arm I, 34.0 of 71.0 in Arm II, and 32.0 of 68.0 in Arm III. Sponsor-reported Cox analyses and unadjusted risk-difference re-calculations do not align exactly; the sponsor’s own analysis takes precedence for the reported trial inference.

Secondary outcomes cover non-relapse mortality, high-dose corticosteroid use, overall survival, and survival without progression. The registry record does not report the original sample-size justification, full statistical analysis plan, multiplicity strategy, or complete handling of missing data. The posted results are best interpreted with attention to the outcome definitions, differing follow-up times, and uncertainty in the reported comparisons.