Study of Posoleucel (Formerly Known as ALVR105; Viralym-M) in Kidney Transplant Patients With BK Viremia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Posoleucel (Formerly Known as ALVR105; Viralym-M) in Kidney Transplant Patients With BK Viremia (NCT04605484), a randomized phase 2 study. The primary outcome is Number of Participants Who Experienced a Treatment-emergent Adverse Event (TEAE).

2. Clinical Question

3. Trial Design

This is a Phase 2, multicenter, randomized, double-blind, placebo-controlled study in kidney transplant recipients with high or low BK viremia. Its official title describes multiple dosing intervals and a 2-period study. The registry identifies a parallel model and quadruple masking. Enrollment was 61. The status is completed.

The study compares posoleucel with placebo. The intervention description identifies posoleucel as multivirus-specific T cells and notes its former names, ALVR105 and Viralym-M. Placebo is described as visually identical to posoleucel. The registry lists three arms: PSL Group 1, PSL Group 2, and Placebo. Separate arm descriptions refer to Regimen A and Regimen B, including a regimen with posoleucel and placebo. Further details about the dosing schedules and how the named regimens correspond to the results groups are not reported in the registry record.

The recorded start date is 2021-03-22, and the primary completion date is 2022-10-20. AlloVir is listed as sponsor. The primary outcome is a count of participants with a treatment-emergent adverse event during Day 1 to Week 24. The primary endpoint description includes untoward medical occurrences temporally associated with study treatment, whether or not considered related to treatment, and clinically significant changes in vital signs, physical examinations, laboratory assessments, and electrocardiograms.

The registry lists change from baseline in BK viral load as a secondary outcome. It reports two outcome measures and one posted secondary outcome, while the record reports no analyses. The registry record does not report the original sample-size justification, detailed allocation procedures, or the statistical plan used for the trial’s own analyses. Those omissions limit what can be inferred about design choices and the intended inferential framework.

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: A total of 82 participants were screened during a 2-week screening period, of which 61 were randomized and received treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Safety Population: Included all participants who received any amount of PSL or placebo.

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: Intent-to-Treat (ITT) Population: Included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Who Experienced a Treatment-emergent Adverse Event (TEAE), measured over Day 1 to Week 24.

The primary endpoint counts participants who experienced at least one treatment-emergent adverse event (TEAE) during Day 1 to Week 24. A TEAE is defined in the registry as an adverse event with a start date and time on or after the first dose through the end of the study. The definition is based on when the event occurred in relation to treatment, not on whether investigators judged it to have been caused by treatment. The endpoint description also includes clinically significant changes in vital signs, physical examinations, laboratory assessments, and electrocardiograms.

This kind of endpoint is used to describe how many participants in each safety group had an event during the stated observation period. It provides a participant-level summary: the reported count concerns participants with an event, rather than a total count of every event occurrence. A participant could experience more than one event, but the primary endpoint as described does not distinguish event frequency or duration.

The safety population includes participants who received any amount of posoleucel or placebo. The posted results report 17 participants with an event in PSL Group 1, 17 in PSL Group 2, and 16 in the placebo group. The corresponding safety-group sizes are 20, 22, and 19. These counts describe event occurrence in this study; on their own, they do not establish whether an event was caused by treatment or whether the groups differ in event type, severity, or clinical importance.

7. Results Posted in the Registry

• PSL Group 1: 85.0% (17/20) versus 84.2% (16/19) on control; risk difference 0.8 percentage points (95% CI -21.9 to 23.5), risk ratio 1.01 (0.77–1.32); unadjusted two-proportion z-test p = 0.946.
• PSL Group 2: 77.3% (17/22) versus 84.2% (16/19) on control; risk difference -6.9 percentage points (95% CI -30.9 to 17.1), risk ratio 0.92 (0.68–1.24); unadjusted two-proportion z-test p = 0.576.

8. Statistical Interpretation

9. Statistical Methods Explained

The posted comparative results use risk differences to compare the proportion of participants with a TEAE in each PSL group against the placebo group. The comparisons are unadjusted. The registry record does not report the statistical methods used in the trial’s original analysis, so the posted estimates should not be treated as a complete account of its prespecified analysis plan.

What does a risk difference represent?

A risk difference subtracts the event risk in one group from the event risk in the comparator group. A positive estimate means the event risk is higher in the group named in the comparison; a negative estimate means it is lower. The reported point estimates have opposite signs: the PSL Group 1 estimate is positive, and the PSL Group 2 estimate is negative. These are absolute contrasts, not relative changes. Their confidence intervals cross the value representing no difference, which means the data do not pin down the direction of the underlying contrast.

The posted results also include relative measures, risk ratios and odds ratios. A risk ratio compares the event risks as a ratio, while an odds ratio compares the odds of an event. Both are relative measures, and their neutral value represents no relative difference. These measures can be harder to interpret than a risk difference because they express a contrast relative to the comparator rather than as an absolute change in risk. Their reported intervals are also wide and encompass the neutral value, reflecting uncertainty in these group comparisons.

How should a p-value be read?

A p-value describes how compatible the observed data are with a specified null model, assuming that model and the analysis conditions are appropriate. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The unadjusted p-values reported for the PSL Group 1 and PSL Group 2 comparisons are 0.946 and 0.576. Those values do not provide evidence against the no-difference model in these individual comparisons. They do not demonstrate that the groups are equivalent, especially because the confidence intervals allow effects in either direction.

Statistical significance and precision are related but distinct. A result can fail to meet a significance threshold because the estimated difference is small, because the data are limited, or because both conditions apply. The confidence intervals are therefore important alongside the p-values: they show a range of effects compatible with the data under the interval method, rather than reducing interpretation to a binary significant-or-not label. The registry record does not report the exact methods used to construct the posted intervals.

Why do event counts and denominators matter?

The endpoint is a count of participants with at least one TEAE. The event counts are interpreted in relation to each group’s safety-population denominator: 17 of 20 in PSL Group 1, 17 of 22 in PSL Group 2, and 16 of 19 in placebo. The denominators matter because counts alone do not describe the proportion of each group affected. The posted comparisons use the group sizes to estimate absolute and relative contrasts. Because the number of participants in each group is limited, even small changes in the event counts could materially affect the estimated group differences.

Participant-level occurrence is different from recurrent-event analysis. The primary endpoint does not count every event as an independent observation, and the posted summary does not describe the number of events per participant. It therefore cannot answer whether one group had more repeated events, longer-lasting events, or a different distribution of event types. The serious adverse event figures are a separate summary and should be interpreted on their own terms.

What can the posted analysis establish?

The results estimate differences in the proportion of participants with at least one TEAE during the specified period. Randomization and masking are features of the study design, but the registry record does not report enough detail to assess every aspect of implementation or analysis. For example, allocation procedures beyond randomized allocation, missing-data rules, and analysis-population rules for the comparative estimates are not reported in the registry record. The safety-population definition is reported, but it does not by itself resolve how missing outcomes or deviations were handled.

The comparisons are against a shared placebo group. When several comparisons use a common comparator, the estimates are not independent of one another. Testing several outcomes or contrasts can also raise the chance of a false-positive finding if multiplicity is not handled. The record identifies the p-values as unadjusted but does not state whether an adjustment was planned or used elsewhere. It is therefore not possible to infer the complete multiplicity strategy from these results alone.

For these reasons, the safest statistical reading is descriptive and contrast-focused: the observed participant counts are close, the estimated risk differences point in opposite directions, and their intervals remain broad and include no difference. The posted p-values do not show clear evidence of a difference in either comparison. These findings are not a formal equivalence assessment, and they do not replace the unreported details of the trial’s own statistical plan.

10. Confidence Intervals and Precision

Confidence intervals communicate how much uncertainty surrounds an estimated group contrast. A narrow interval would indicate a more precisely estimated effect; a broad interval indicates that a wide range of effects remains compatible with the data and the method used to calculate the interval. The intervals reported for both risk differences are broad and cross no difference. They extend into both negative and positive values, so the direction of the underlying difference is uncertain.

The same caution applies to the relative measures. The risk-ratio and odds-ratio intervals cover their respective neutral values, and the ranges are broad. This means the results do not precisely distinguish between a relative reduction, little or no difference, or a relative increase in TEAE risk. The p-values do not remove that uncertainty; they address a different question about compatibility with a null model.

Group sizes are 20 for PSL Group 1, 22 for PSL Group 2, and 19 for placebo. These denominators, together with the event counts, help explain why the estimates are not highly precise. With a limited number of observations, each participant’s outcome can have a noticeable influence on the estimated contrast. The confidence intervals are therefore more informative than a simple statement that a comparison was or was not statistically significant.

Precision is not the same as clinical importance. The interval width describes statistical uncertainty, while deciding what differences would matter requires context and a prespecified threshold. The registry record does not report a threshold for a clinically important difference, nor a margin for equivalence or non-inferiority. The results consequently support cautious interpretation of the observed safety comparisons, not a conclusion that clinically meaningful differences have been ruled out.

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 sample-size illustrations translate the observed risk-difference estimates into planning scenarios. The listed figures are participants per arm, not total participants across a study. They are based on two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a future study to have an 80% chance of detecting the chosen effect under the stated planning assumptions, if that effect is the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are design targets, not guarantees: actual results depend on the true effect, event rates, data quality, and whether the assumptions are met.

Each comparison has its own observed effect and therefore its own planning values. For PSL Group 1, planning for 100% of the observed effect gives 32,804 participants per arm for 80% power and 43,914 for 90% power. Planning for 75% gives 58,624 and 78,480, while planning for 50% gives 132,589 and 177,499. For PSL Group 2, the corresponding figures are 506 and 677 for 100%, 870 and 1,163 for 75%, and 1,885 and 2,522 for 50%.

Smaller effects require more participants to detect under the same assumptions, which is why the planning figures rise as the assumed fraction of the observed effect falls. These calculations are not observed power. They are planning illustrations derived from the observed effects, not evidence about the trial’s actual power or a record of its original design.

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 = 0.842; treatment proportion p₁ = 0.850; average p̄ = 0.846.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5104 = 1.0003.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5104 = 0.4295.
4. n = (1.0003 + 0.4295)² / (0.0079)² = 32,803.2, rounded up to 32,804 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 <- 0.842105263157895                          # control proportion
p1 <- 0.85                          # 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(4605484)
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 = 32,804 (80% power), 43,914 (90% power)
 75% of observed effect: n per arm = 58,624 (80% power), 78,480 (90% power)
 50% of observed effect: n per arm = 132,589 (80% power), 177,499 (90% power)
power.prop.test: 32803.2 
Simulated power at n = 32,804 per arm: 0.799 (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 record reports two posted outcome measures, one posted secondary outcome, and no analyses. It identifies change from baseline in BK viral load as a secondary outcome, but does not report an analysis for that measure in the results. The record also does not report whether additional outcomes or comparisons were prespecified or how they were ranked for interpretation.

The two posted risk-difference comparisons each use placebo as the comparator. The reported p-values are unadjusted. The registry record does not report whether a multiplicity correction was planned or applied, or whether the reported comparisons were the only inferential tests conducted. When several comparisons or outcomes are considered, multiplicity matters because repeated testing can increase the chance of at least one false-positive result. Without the analysis plan, the appropriate family of tests and any adjustment cannot be established.

Information about missing data is not reported in the registry record. The record does not describe how participants without an evaluable outcome were handled, whether any outcomes were missing, or whether sensitivity analyses were conducted. The reported safety population includes participants who received any amount of posoleucel or placebo, but the record does not explain how this population was applied to each comparative analysis.

The registry record also does not report the primary analysis model, any covariate adjustment, the method used to form confidence intervals, or any interim analyses. These details should not be inferred from the posted risk differences and p-values. Their absence limits assessment of whether the comparisons reflect the original analysis plan and how robust the results are to alternative assumptions.

As a result, the posted figures are best read as individual unadjusted comparisons with substantial uncertainty. They do not provide a complete account of missing-data handling, multiplicity, or the full analysis populations. A formal claim about the study’s overall evidence requires those elements of the analysis plan, which are not reported in the registry record.

14. 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: pyelonephritis (5.0%), renal tuberculosis (5.0%), urosepsis (5.0%), acute respiratory failure (5.0%), transplant rejection (4.5%).

The serious adverse event summary reports 2 affected participants among 20 at risk in PSL Group 1, 2 among 22 in PSL Group 2, and 0 among 19 in the placebo group. These are participant counts for serious events, not the broader primary endpoint count of participants with any TEAE. The registry also reports zero deaths in each group.

The listed serious-event terms include Pyelonephritis, Renal tuberculosis, Urosepsis, and Acute respiratory failure, each reported as 5.0%. Transplant rejection and Enterococcal bacteraemia are each reported as 4.5%. These term percentages should be read as listed in the registry; the record does not provide further detail about how repeated terms in a participant were counted or how the term-level percentages were calculated.

These summaries are descriptive. The group sizes are limited, and the registry does not report a comparative statistical analysis of serious events. A count of zero in one group does not establish that the event cannot occur, while the small counts do not support a precise estimate of relative risk. Serious-event counts also do not determine whether an event was caused by study treatment. The event definitions, clinical context, and assessment of relatedness would be needed to interpret individual events beyond these posted summaries.

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

The posted results show that TEAEs were reported among participants in both posoleucel groups and the placebo group during Day 1 to Week 24. The group counts are 17 of 20 for PSL Group 1, 17 of 22 for PSL Group 2, and 16 of 19 for placebo. The estimated risk difference is positive for the first comparison and negative for the second. The reported unadjusted p-values do not indicate a clear statistical difference from placebo in either comparison.

That pattern is not proof that the groups have the same safety profile. The confidence intervals are broad and include no difference as well as effects in both directions. The study’s posted safety results therefore leave meaningful uncertainty about the size and direction of the group contrasts. They also do not establish equivalence or non-inferiority, because the registry record does not report a margin or an analysis designed to test either claim.

The primary endpoint captures whether a participant had at least one TEAE, including events not considered related to treatment. It does not, by itself, describe recurrent events, duration, severity distribution, or the cause of each event. The separate serious-event summary reports few affected participants and zero deaths in the posted groups, but those data are also descriptive and limited in precision.

The registry lists change from baseline in BK viral load as a secondary outcome, but no analysis of that outcome is reported in the available record. The safety findings therefore cannot answer questions about viral-load change. More generally, the results apply to the trial’s kidney transplant recipient population and study conditions; the record does not support extrapolation to other populations, settings, or schedules.

The clearest conclusion is statistical rather than clinical: the posted counts are close, the estimated contrasts do not point in the same direction, and the intervals leave substantial uncertainty. The results do not show a clear difference in the reported comparisons, but they also do not rule out differences that could matter. Further interpretation depends on the complete analysis plan and clinical context, neither of which is fully reported in the registry record.

16. Why This Trial Matters Statistically

This trial illustrates why event counts, effect estimates, and uncertainty should be read together. The raw TEAE counts are close across the three groups, but counts alone do not account for differences in group size. The comparative estimates put the groups on a common scale, while the confidence intervals show that the underlying differences remain uncertain.

The two posoleucel-versus-placebo estimates point in opposite directions. That feature cautions against treating one comparison as a general summary of all posoleucel exposure. The registry describes different regimens, but it does not provide enough detail in the posted information to explain the regimen distinctions or connect them to the comparative results. Statistical interpretation needs to preserve those separate contrasts rather than combine them without an analysis plan.

It also matters that the primary outcome is a broad safety measure. A participant is counted if a qualifying TEAE occurs, regardless of whether it was considered related to study treatment. This approach captures a wide range of events, but it does not describe the frequency of repeated events or establish causation. The separate serious-event summary adds a different perspective, but the counts remain small and descriptive.

The planning illustrations make the role of effect size visible: targeting smaller effects requires larger studies under the stated assumptions. They should not be mistaken for evidence that the completed trial had a particular power or that its original design used those assumptions. The original sample-size justification is not reported in the registry record.

Together, these features show why a non-significant comparison is not a finding of equivalence, and why an observed difference is not, by itself, proof of a causal effect. The registry results support a careful account of what was observed while leaving substantial uncertainty about the true comparative safety profile.

17. 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 comparative safety results have limited precision. The group sizes are 20, 22, and 19, and the confidence intervals for the risk differences are broad. The estimates are therefore sensitive to the outcomes of individual participants and do not tightly determine the direction or size of a group difference.

The primary endpoint is a count of participants with at least one TEAE. It does not distinguish the number of events per participant, event duration, or the full distribution of severity. Although the endpoint definition includes clinically significant changes in several clinical assessments, the registry record does not provide event-level detail sufficient to evaluate those components separately. The event counts also include occurrences whether or not considered related to treatment.

The registry record does not report the trial’s original sample-size rationale, detailed statistical analysis plan, missing-data approach, or multiplicity strategy. It also does not report the method used to calculate the comparative confidence intervals. The p-values are unadjusted, and the record reports no analyses for the listed secondary outcome of change from baseline in BK viral load. These omissions constrain assessment of the full planned evidence and the robustness of the posted comparisons.

The intervention descriptions refer to Regimen A and Regimen B, including a regimen with posoleucel and placebo, but the registry record does not give further dosing details or explicitly map those regimens to the PSL Group 1 and PSL Group 2 results in the information analyzed. This limits interpretation of differences between the two PSL groups.

Finally, the serious-event counts are descriptive and sparse. The registry’s listed event terms and percentages do not supply enough detail to infer comparative risks or causation. These results should be understood as a limited set of posted summaries from a completed Phase 2 study, not as a complete characterization of all safety or viral-load outcomes.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Study of Posoleucel (Formerly Known as ALVR105; Viralym-M) in Kidney Transplant Patients With BK Viremia — NCT04605484.
• Registry record last updated 2024-05-16; status last verified 2024-04.
• Results first posted 2024-05-16.
• 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.

21. Record Summary

NCT04605484 is a completed Phase 2, multicenter, randomized, double-blind, placebo-controlled study of posoleucel in kidney transplant recipients with high or low BK viremia. The registry describes a parallel model, quadruple masking, and enrollment of 61. The recorded start date is 2021-03-22, and the primary completion date is 2022-10-20. AlloVir is listed as sponsor.

The primary endpoint counts participants with a treatment-emergent adverse event from Day 1 to Week 24. The posted counts are 17 in PSL Group 1, 17 in PSL Group 2, and 16 in placebo. The unadjusted comparisons do not show clear evidence of a difference, and their confidence intervals are broad. The registry lists change from baseline in BK viral load as a secondary outcome but reports no analysis for it in the record analyzed.

The record does not report the original sample-size justification, full statistical plan, missing-data handling, or multiplicity strategy. The results are therefore best read as descriptive and imprecise safety comparisons, rather than as evidence of equivalence or a complete account of the study’s planned analyses.