Influenza Vaccine Post Allogeneic Transplant: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Influenza Vaccine Post Allogeneic Transplant (NCT01215981), a randomized na study. The primary outcome is Number of Subjects With T-Cell Based Immune Response to Vaccine.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-center, parallel-group study of seasonal influenza vaccine immune responses after allogeneic hematopoietic stem cell transplantation. Its official title asks whether one or two vaccine doses are needed to assess influenza-vaccine-specific immune responses after transplant. The study record lists phase as not applicable, allocation as randomized, and masking as none. The listed enrollment is 68. The study began in 2010-09, had primary completion in 2011-06, and its status is terminated.

The two transplant-recipient groups were assigned to one vaccine dose or two vaccine doses. The study description says the two doses were given one month apart. The arm descriptions specify that transplant recipients were more than 60 days post-transplant. The one-dose arm description also includes healthy adult volunteers meeting listed eligibility criteria. The registry describes these volunteers as a control cohort intended to confirm immune response to a single influenza vaccine. However, the posted primary outcome comparison is between transplant recipients randomized to one versus two doses; it does not include a healthy-volunteer arm.

The primary endpoint was assessed eight weeks after vaccination. The registry also lists an H3-based immune response at the same timeframe as a secondary endpoint. The posted primary outcome counts are based on 32 evaluable participants in each transplant-recipient arm. The record notes that one of the 33 participants randomized to one dose died before the eight-week evaluation. It does not give further details about that death in the outcome description.

The record does not report the random-sequence generation method, allocation concealment procedures, eligibility details beyond those in the arm descriptions, or the reason the study was terminated. It also does not report the original sample-size justification or a detailed statistical analysis plan. Those omissions limit assessment of design choices beyond the listed randomization, parallel allocation, masking status, groups, and 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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: One of the 33 participants randomized to receive 1 vaccine dose died prior to the 8 week evaluation.

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 Subjects With T-Cell Based Immune Response to Vaccine, measured over 8 Weeks After Vaccination.

The primary endpoint is the number of participants with a T-cell-based immune response to the influenza vaccine, assessed eight weeks after vaccination. The registry defines a response as a laboratory result four times above background after a filter plate was developed. The outcome is therefore a binary classification at the participant level—meeting or not meeting the stated response criterion—reported as a count of evaluable participants who responded.

An immune-response endpoint is used to characterize a biological response to vaccination. It is not itself a clinical endpoint such as a count of influenza infections, hospitalizations, or other patient-important events. The registry record does not report those outcomes as primary endpoints. Consequently, the posted result addresses the measured laboratory response, not whether participants experienced fewer influenza infections or other clinical outcomes.

For the primary comparison, the registry lists 14 responders among 32 evaluable transplant recipients randomized to one dose, and 15 among 32 randomized to two doses. The reported risk difference is 0.031, with a confidence interval from -0.212 to 0.275. The estimate describes the observed contrast in response proportions, while the interval conveys substantial uncertainty around that contrast. Interpretation should keep the laboratory definition, assessment time, and evaluable population in view.

7. Results Posted in the Registry

• HSCT Recipients Who Were Randomized to 2 Vaccine Doses: 46.9% (15/32) versus 43.8% (14/32) on control; risk difference 3.1 percentage points (95% CI -21.3 to 27.5), risk ratio 1.07 (0.63–1.84); unadjusted two-proportion z-test p = 0.802.

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 Subjects With H3 Based Immune Response to Vaccine

• 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:
  • HSCT Recipients Who Were Randomized to 2 Vaccine Doses: 21.9% (7/32) versus 12.5% (4/32) on control; risk difference 9.4 percentage points (95% CI -9.0 to 27.7), risk ratio 1.75 (0.57–5.40); unadjusted two-proportion z-test p = 0.320.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HSCT Recipients Who Were Randomized to 2 Vaccine Doses and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: the number of subjects with an H3-based immune response to vaccine, assessed eight weeks after vaccination. Its posted comparison follows the same broad pattern as the primary endpoint in that it is a laboratory response count comparing transplant recipients randomized to one versus two doses. The estimates remain uncertain, and the posted results do not establish a clear difference between the dose groups.

The secondary outcome can add context to the T-cell-based primary result because it measures a different specified immune-response outcome. It does not independently confirm a clinical benefit, since the registry reports immune-response counts rather than influenza illness or other clinical endpoints. Nor should the two outcomes be treated as interchangeable: they use distinct response definitions, and each addresses its own laboratory measure.

Unadjusted secondary results generally carry less weight than a prespecified primary result when multiple outcomes are considered. As a general statistical issue, examining multiple endpoints creates more opportunities for an apparently notable result to arise by chance, unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity plan, a hierarchy for testing outcomes, or a detailed statistical analysis plan. It also lists no reported analyses. Therefore, the secondary result is best treated as supportive descriptive information, not as a standalone basis for a strong confirmatory conclusion.

Interpretation should also account for the limited precision of the posted estimates and the fact that both outcomes are assessed at the same stated time after vaccination. The registry record does not report additional timepoints or other secondary outcome results. The overall pattern is thus confined to the posted laboratory endpoints and does not establish how immune responses relate to clinical outcomes.

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

• Number of Subjects With H3 Based Immune Response to Vaccine

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each evaluable participant either met the registry’s laboratory response definition or did not. The posted counts can therefore be described as response proportions, and the primary contrast is reported as a risk difference. A risk difference expresses the absolute difference between the two groups’ response proportions, with the comparison oriented in the registry results as two doses relative to one dose. A value of zero represents no difference in the proportions. Positive or negative values indicate the direction of the contrast under that orientation.

What does the risk difference describe?

The posted estimate is 0.031, with a confidence interval from -0.212 to 0.275. The estimate is a summary of the observed contrast, not a guarantee of the contrast that would occur in another study. Because the interval crosses zero and extends in both directions, the observed data do not narrowly identify the direction or size of a possible difference. The interval is considered alongside the point estimate rather than replaced by it.

The record also gives a risk ratio and an odds ratio. These are relative measures, unlike the risk difference, which is an absolute measure. The risk ratio compares the two response proportions as a ratio. The odds ratio compares the odds of response between groups. The reported risk ratio is 1.071, with a confidence interval from 0.625 to 1.837, and the odds ratio is 1.134, with a confidence interval from 0.424 to 3.037. Relative measures can be useful for describing contrasts, but they do not remove the uncertainty in the small set of observed counts. Their interpretation also depends on the chosen scale.

How should the p-value be read?

The unadjusted p-value for the primary comparison is 0.802. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions used for the test. It is not the probability that the null hypothesis is true, and it does not quantify the probability that a result will replicate. A large p-value does not prove that the groups are equivalent. In this study, the p-value should be read with the estimated difference and its confidence interval, which show that the data are not precise enough to distinguish among a range of possible effects.

The record does not report a named statistical test, covariate adjustment, or a detailed analysis specification. The displayed comparisons are unadjusted. The registry lists no reported analyses, so it is not possible to determine whether the posted comparisons reproduce a prespecified analysis or whether other analyses were conducted but not entered in the record. The registry record does not report interim analyses, stopping rules, or a plan for handling multiple outcomes.

Why can over-dispersion matter?

Over-dispersion is a general concern when observed variation exceeds what a chosen statistical model expects. It is especially relevant to count outcomes analyzed with models that assume a particular relationship between the mean and variance. Greater-than-expected variability can make standard errors too small if it is ignored, producing confidence intervals that are too narrow and tests that appear more decisive than warranted. The posted primary endpoint is a binary participant count, and no dispersion estimate or count-model analysis is reported. Over-dispersion is therefore a general statistical concept rather than a documented feature of this analysis.

For binary outcomes, the number of participants and the number meeting the response definition both affect precision. The primary comparison has 32 evaluable participants in each arm, with 14 and 15 responders. With counts of this size, a small change in the number classified as a responder could alter the estimated proportions. The confidence interval communicates this sampling uncertainty; the point estimate by itself does not.

The registry’s primary response definition uses a laboratory threshold: a response is four times above background after development of a filter plate. Any such threshold converts an underlying biological measurement into a response/no-response classification. As a general matter, dichotomizing a measurement can make results easier to summarize but discards information about values within each category and how far observations lie from the threshold. The registry does not report continuous laboratory values, threshold validation details, or alternative definitions, so their influence cannot be assessed.

Random allocation is intended, in general, to balance measured and unmeasured participant characteristics across groups on average, but a randomized design does not ensure balance in every realized sample. The registry identifies the study as randomized and unmasked, but does not describe the randomization procedure or concealment. With the posted group sizes, chance imbalance remains possible. Since no adjusted analyses or baseline characteristics are reported in the outcome information, the posted comparison is interpreted as the unadjusted contrast between the randomized groups rather than a covariate-adjusted effect estimate.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data identify an effect estimate. For the primary risk difference, the estimate is 0.031 and its confidence interval ranges from -0.212 to 0.275. The interval includes zero and values on either side. This means the observed estimate is compatible with a range of possible differences; the data do not pin down a precise direction or magnitude. A confidence interval is not a range containing a fixed proportion of individual responses. In general, it is a method for expressing uncertainty in an estimate under the assumptions of the analysis.

The relative measures tell a similar story of uncertainty. The risk ratio is 1.071, with a confidence interval from 0.625 to 1.837. The odds ratio is 1.134, with a confidence interval from 0.424 to 3.037. The intervals span a range of relative effects, so neither point estimate should be read as a precise or settled description of the underlying contrast. The risk difference and relative measures express effects on different scales; their numerical values are not directly interchangeable.

The secondary H3-based response estimate also has a confidence interval extending across zero for its risk difference: 0.094, with limits from -0.090 to 0.277. This is likewise an imprecise estimate. Precision should be distinguished from whether an estimate is above or below zero: an estimate can have a positive point value while still being uncertain about the direction of the underlying difference.

The primary outcome counts 32 evaluable participants in each group. The registry records one death before evaluation among the 33 participants randomized to one dose. Small groups and limited responder counts leave the estimates sensitive to the observed outcomes, and the confidence intervals reflect substantial uncertainty. The registry record does not report a target precision or a prespecified margin for an acceptable difference.

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 illustrations are planning calculations based on the observed effect, not the trial’s original design assumptions. For these binary outcomes, the listed values are participants per arm, rather than total events. The planning 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 registry record does not report the original sample-size justification, so these illustrations should not be interpreted as the study’s planned enrollment target.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the stated effect under those planning assumptions, if that effect were the true effect. The 90% power column expresses the corresponding planning target for a 90% chance. These are design characteristics for hypothetical future studies; they do not describe the probability that the current study detected an effect. This is not observed power.

The rows that use 75% or 50% of the observed effect illustrate planning for smaller effects than the observed estimate. Smaller effects generally require more participants to distinguish them from no difference with the same significance level and power target. The values should therefore be read as conditional illustrations, not recommendations or guarantees. A real study’s design would also need to consider its intended population, endpoint definition, analysis plan, and other protocol choices, which are not fully reported in the registry record.

In general, a sample-size curve displays how the required number of participants changes as the effect to detect changes. Read the curve by matching an assumed effect with the corresponding planned sample size and power target. The curve does not show the number enrolled in this study, the number who responded, or the probability that the study’s result is correct. Here the illustrations are based on the posted observed effects, so they are particularly sensitive to uncertainty in those estimates.

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 = 0.438; treatment proportion p₁ = 0.469; average p̄ = 0.453.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7040 = 1.3798.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7036 = 0.5922.
4. n = (1.3798 + 0.5922)² / (0.0312)² = 3,982.1, rounded up to 3,983 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 <- 0.4375                          # control proportion
p1 <- 0.46875                          # 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(1215981)
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 = 3,983 (80% power), 5,331 (90% power)
 75% of observed effect: n per arm = 7,070 (80% power), 9,464 (90% power)
 50% of observed effect: n per arm = 15,882 (80% power), 21,260 (90% power)
power.prop.test: 3982.1 
Simulated power at n = 3,983 per arm: 0.801 (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 lists a primary T-cell-based immune-response outcome and one secondary H3-based immune-response outcome. It does not report whether hypotheses were tested in a fixed order, whether an adjustment for multiple comparisons was planned, or whether either endpoint was exploratory. When multiple outcomes are analyzed, the chance of at least one apparently unusual result can increase. In general, a prespecified multiplicity strategy can help control that issue, but no such strategy is reported in the registry record. The secondary result should therefore be interpreted cautiously alongside the primary result.

The outcome description identifies one participant randomized to one dose who died before the eight-week evaluation. The posted primary analysis includes 32 evaluable participants in that arm, compared with 32 in the two-dose arm. The record does not report an imputation method, a missing-data sensitivity analysis, or whether the primary analysis followed an intention-to-treat principle. It also does not explain the circumstances or cause of the death. Because the primary endpoint is defined at the eight-week assessment, the absence of an evaluation for this participant affects the distinction between the randomized group and the evaluable group.

The posted counts are described as evaluable participants who successfully responded. The registry does not report details about any other missing measurements, exclusions after randomization, or how the evaluable population was determined. It is not possible to infer from the outcome counts whether all other randomized participants had complete endpoint data or how any incomplete laboratory results were handled.

The record identifies the trial as randomized and unmasked, but does not report sequence generation, allocation concealment, interim analyses, stopping rules, or the original statistical analysis plan. It reports no formal analyses. These missing details limit assessment of prespecification and analytic choices. They do not alter the reported counts, but they restrict how fully the results can be evaluated for selective analysis, missing-data handling, and multiplicity.

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.

The registry lists serious adverse events and other adverse events separately for the transplant-recipient groups. In the one-dose group, the record lists zero serious events among 33 at risk and zero other events among 33 at risk. In the two-dose group, it lists zero serious events among 32 at risk and zero other events among 32 at risk. No serious-event terms are listed.

These entries mean that no events are recorded in those adverse-event categories in the posted registry results. They should not be read as proof that no adverse experiences occurred or that uncommon events could be excluded. The record does not provide additional event definitions or detail about safety monitoring. It also does not report deaths in the adverse-event fields. Separately, the primary outcome description notes that one participant randomized to one dose died before the eight-week assessment, but the reason and relationship to vaccination are not reported in the registry record. The adverse-event counts and that endpoint note are distinct pieces of information and should not be conflated.

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

The posted results describe immune-response measurements after influenza vaccination among transplant recipients randomized to one or two doses. For the primary T-cell-based endpoint, the observed counts are 14 responders among 32 evaluable participants in the one-dose group and 15 among 32 in the two-dose group. The estimated risk difference is 0.031, and its confidence interval includes values in either direction. The evidence is therefore too imprecise to establish a clear difference between these groups in the measured response.

This result does not show that the dose strategies are equivalent. Equivalence requires a prespecified margin and a design and analysis intended to establish that differences fall within that margin; the registry record does not report such a framework. The result also does not establish noninferiority, which likewise requires a defined margin and appropriate planning. A nonsignificant or imprecise comparison is not, by itself, evidence that two approaches have the same effect.

The endpoint is a laboratory immune-response definition at eight weeks, not a count of influenza infections or other clinical events. The posted results cannot establish whether either dose strategy changes the risk of influenza illness, complications, or other outcomes not reported as endpoints. The registry’s secondary H3-based response is also an immune-response measure and does not fill that gap.

The adverse-event entries record zero serious and zero other events in the listed groups, but the event counts do not demonstrate the absence of risk. The study’s enrollment and the posted group sizes provide limited information about rare events, and the registry does not give additional safety detail. In addition, the record notes one death before the primary assessment without reporting its cause or relationship to vaccination.

These findings should be understood as a description of the posted data for a specific transplant-recipient comparison. They do not support medical advice or a recommendation about vaccine dosing. The registry record does not provide a complete protocol, original sample-size rationale, or detailed analysis plan, and it is not possible to infer unreported clinical outcomes or analyses.

17. Why This Trial Matters Statistically

This study illustrates an important distinction between a biological endpoint and a clinical outcome. The primary endpoint counts participants meeting a laboratory response criterion, which can be useful for describing immune response. That measure is not equivalent to demonstrating a change in influenza illness or another clinical event. Statistical interpretation must stay aligned with what the endpoint actually records.

It also illustrates why an estimated difference and its precision should be read together. The primary point estimate is 0.031, but its confidence interval extends from -0.212 to 0.275. A point estimate can look close to no difference while the interval still allows a wide range of possible effects. The unadjusted p-value of 0.802 does not resolve that uncertainty or establish equivalence.

The evaluable population matters as well. The one-dose group includes 32 participants in the posted endpoint result, while the registry notes that 33 were randomized and one died before the assessment. Distinguishing randomized participants from those with an observed endpoint is essential when interpreting outcome counts and considering missing data.

Finally, the registry record leaves several design and analysis details unreported, including the original sample-size justification, multiplicity strategy, and missing-data methods. These gaps do not erase the observed counts, but they shape what can be concluded from them. The study is a useful example of how a randomized comparison can produce descriptive estimates while still leaving substantial uncertainty about the magnitude, direction, and clinical meaning of the contrast.

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 posted primary comparison is based on 32 evaluable transplant recipients per group. The registry notes that one of 33 participants randomized to one dose died before the eight-week evaluation. It does not report the circumstances, cause, or relationship of the death to vaccination, nor does it describe a method for handling the missing primary assessment. This makes it important to distinguish the observed endpoint population from the randomized group.

The endpoint is a laboratory response classification at a single stated timepoint. The registry does not report continuous assay measurements, validation information for the threshold, or outcomes such as influenza illness. The results therefore have a narrower scope than clinical effectiveness. The healthy-volunteer control cohort described in the study summary is not represented in the posted primary outcome arms, limiting interpretation to the transplant-recipient dose comparison.

The trial is identified as terminated, but the reason is not reported in the registry record. The record also does not report the original sample-size justification, a detailed statistical analysis plan, random-sequence generation, allocation concealment, interim analyses, or a multiplicity strategy. No formal analyses are listed. These omissions limit evaluation of whether the posted analyses were prespecified and how other possible analyses were handled.

The reported adverse-event entries contain zero events in the listed categories, but the registry offers no further safety detail. The posted outcomes also do not establish equivalence or noninferiority, and they do not describe clinical outcomes beyond immune-response measures. These limitations constrain the conclusions to the observed laboratory response counts and their uncertainty.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Influenza Vaccine Post Allogeneic Transplant — NCT01215981.
• Registry record last updated 2017-12-28; status last verified 2017-12.
• Results first posted 2016-08-16.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a randomized, unmasked, parallel-group, single-center study of seasonal influenza vaccine immune responses after allogeneic hematopoietic stem cell transplantation. It compares transplant recipients assigned to one or two doses, with the study description stating that two doses were given one month apart. The listed enrollment is 68, and the record status is terminated.

The primary endpoint is the number of evaluable participants with a T-cell-based immune response eight weeks after vaccination. The posted comparison includes 14 responders among 32 participants in the one-dose group and 15 among 32 in the two-dose group. The risk-difference estimate is 0.031, with a confidence interval from -0.212 to 0.275. One secondary H3-based immune-response outcome is also listed. The registry record does not report the original sample-size justification, a detailed statistical analysis plan, or the reason for termination.