Study of Efficacy, Safety, Tolerability, Pharmacokinetic (PK) and Pharmacodynamic (PD) of an Anti-CD40 Monoclonal Antibody, CFZ533, in Liver Transplant Recipients With Additional 12-month Follow-up and Long-term Extension: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Efficacy, Safety, Tolerability, Pharmacokinetic (PK) and Pharmacodynamic (PD) of an Anti-CD40 Monoclonal Antibody, CFZ533, in Liver Transplant Recipients With Additional 12-month Follow-up and Long-term Extension (NCT03781414), a randomized phase 2 study. The primary outcome is Percentage of Patients With Composite Event (Biopsy Proven Acute Rejection (BPAR), Graft Loss or Death) Over 12 Months.

2. Clinical Question

3. Trial Design

CONTRAIL I was a Phase 2, multicenter, randomized, open-label, active-controlled, parallel-group study in adult de novo liver transplant recipients. It evaluated two CFZ533 maintenance regimens against TAC with MMF and CS. The registry record lists enrollment of 129 and a terminated study status. The listed study start was 2019-10-07, and primary completion was 2023-04-20.

The 300 mg CFZ533 regimen comprised a single 30 mg/kg intravenous loading dose on Day 8, followed by subcutaneous 300 mg every 2 weeks beginning on Day 29, in combination with MMF and CS. The 600 mg regimen comprised a 30 mg/kg intravenous loading dose on Day 8 and a 15 mg/kg dose on Day 15, followed by subcutaneous 600 mg every 2 weeks beginning on Day 29, also with MMF and CS. Both regimens were described as continuing up to the end of study. TAC control combined TAC, MMF and CS.

For the primary outcome, the posted analysis population was the Full Analysis Set. The listed group sizes were 48 for the 300 mg regimen, 48 for the 600 mg regimen, and 32 for TAC control. These are the primary-outcome group counts; the registry record does not explain the relationship between these counts and the total enrollment. The treatment assignments were unmasked, so participants and study personnel were not blinded according to the record.

The study also listed secondary outcomes for change in estimated glomerular filtration rate from randomization to Month 12, treatment-emergent adverse events, and dose interruptions or permanent discontinuation. Further detail about the study’s original design assumptions, allocation procedures, or statistical analysis plan is not reported in the registry record.

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: Patients were randomized at a ratio of 2:3:3 to TAC Control (Arm 1) or one of two maintenance regimens of CFZ533: 600 mg CFZ533 subcutaneous (SC) injections every 2 weeks (Arm 2) or 300 mg CFZ533 SC injections every 2 weeks (Arm 3) combined with MMF and CS.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS)

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 Percentage of Patients With Composite Event (Biopsy Proven Acute Rejection (BPAR), Graft Loss or Death) Over 12 Months, measured over Baseline to Month 12.

The primary endpoint counted participants who experienced at least one component of a composite event from baseline to Month 12: biopsy proven acute rejection, graft loss, or death. It is a participant count, rather than a measure of the number of repeated events. The record states that BPAR was assessed by central pathologist evaluation, whereas graft loss and death were assessed locally.

A composite endpoint combines clinically distinct outcomes into one measure. In general, this can capture more than one way a participant may have an unfavorable course and can make a study outcome less dependent on a single event type. The trade-off is that the combined result does not by itself show which component drove the observed count. The posted primary results do not provide component-specific counts, so the contribution of BPAR, graft loss, and death cannot be separated from these results.

The endpoint is reported for the Full Analysis Set and compares each CFZ533 regimen with TAC control. The registry record labels the sponsor analyses as non-inferiority analyses. However, it does not report the non-inferiority margin or the detailed decision rule, so the endpoint counts and estimates alone do not establish how the formal non-inferiority conclusion was defined.

7. Results Posted in the Registry

• CFZ533 300 mg Regimen (CFZ533 300 mg + MMF): 16.7% (8/48) versus 9.4% (3/32) on control; risk difference 7.3 percentage points (95% CI -7.3 to 21.9), risk ratio 1.78 (0.51–6.20); unadjusted two-proportion z-test p = 0.354.
• CFZ533 600 mg Regimen (CFZ533 600 mg + MMF): 25.0% (12/48) versus 9.4% (3/32) on control; risk difference 15.6 percentage points (95% CI -0.3 to 31.5), risk ratio 2.67 (0.82–8.71); unadjusted two-proportion z-test p = 0.079.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a binary participant-level measure: each participant is classified according to whether the composite event occurred during the stated timeframe. The analysis compares the proportion or rate of participants with an event in a CFZ533 group with that in TAC control. The registry record describes the outcome as a count of participants and gives the Full Analysis Set as the analysis population.

What does a risk difference describe?

A risk difference expresses the difference between the event proportions in two groups. A value above zero indicates a higher observed event proportion in the first group as ordered in the comparison; a value below zero indicates a lower one. A value near zero indicates little observed difference on this scale. The unadjusted re-calculations are based on the posted group counts and do not adjust for other variables. They are descriptive checks rather than a substitute for the sponsor’s analysis.

The registry record’s sponsor analyses are described as rate differences and are labeled non-inferiority analyses. A rate difference and a simple difference between observed proportions need not be identical estimands or be calculated using identical methods. The statistical method for the sponsor estimates is not specified in the record. The non-inferiority margin, the hypotheses used, and the decision rule are also not reported, so those features cannot be reconstructed from the label alone.

How should a p-value be read?

A p-value describes how compatible data are with a specified null model, under the assumptions of the test. It does not measure the probability that a treatment effect is true, nor does it describe the magnitude or practical importance of an effect. The re-calculated p-values are unadjusted, simple comparisons based on summary counts. The record does not identify a method for those calculations as the sponsor’s prespecified method, and the values should not be used to infer the sponsor’s non-inferiority conclusion.

In general, a non-inferiority analysis asks whether the data rule out a loss larger than a prespecified acceptable margin. That question depends on the margin, the direction of comparison, and the confidence interval relative to the margin. Since the margin and detailed statistical plan are not reported in the registry record, the posted non-inferiority label cannot be independently assessed from the available details alone.

What does the confidence interval add?

A confidence interval gives a range of effect values compatible with the data under the method used. It communicates precision as well as the direction and size of the estimate. A broad interval indicates that the data are consistent with a wider range of possible effects; a narrow interval indicates greater precision. Whether an interval supports non-inferiority depends on its relation to the prespecified margin, not merely on whether it includes zero. The sponsor’s posted analyses include 95% confidence intervals, while the simple re-calculations have their own intervals. They should not be treated as interchangeable when the estimands or methods differ.

Counts are also important to interpretation. The primary comparison has 48 participants in each CFZ533 group and 32 in control. With limited event counts, changing the outcome status of a small number of participants can materially affect an estimate. This is a general feature of binary outcomes in small groups, not evidence that any particular participant’s classification was wrong.

What analysis details are missing?

The registry record does not report the sponsor analysis method, the non-inferiority margin, the handling of missing primary outcomes, details of the allocation procedure, or a full statistical analysis plan. It also does not report interim analyses. The primary population is identified as the Full Analysis Set, but the record does not provide enough detail to assess the exact inclusion rules or how participants with incomplete outcome information were handled. These omissions limit independent reproduction and interpretation of the formal analysis.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the effect, rather than whether an estimate is statistically significant. The sponsor’s posted analyses include 95% confidence intervals for the rate difference. The interval for the 300 mg comparison extends across zero; the interval for the 600 mg comparison is reported zero. The simple re-calculations are a separate, unadjusted analysis and should not be conflated with those sponsor intervals.

In general, a confidence interval represents a range of values compatible with the data and the statistical method used. A wide interval means the estimate is uncertain across a broader range; a narrow interval indicates greater precision. For a non-inferiority question, the relevant comparison is with the prespecified non-inferiority margin. That margin is not reported in the registry record, so the intervals cannot be judged against it from the posted information.

The group sizes and event counts help explain why precision matters. The primary outcome lists 8 events among 48 participants for the 300 mg regimen, 12 among 48 for the 600 mg regimen, and 3 among 32 in control. The control group is smaller, and the total number of observed composite events is limited. These features mean that the estimates can be sensitive to a small number of outcome classifications. The registry record does not provide component-specific intervals or missing-data sensitivity analyses, so precision for individual components and robustness to missing outcomes cannot be evaluated from the posted results.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For these binary-outcome comparisons, the entries are participants per arm, not total events. The stated illustration assumptions are two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm under the illustration assumptions for a design intended to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher target chance of detecting that effect, under the same stated framework. These are planning concepts, not guarantees about a particular trial. The figures are not observed power.

The rows labeled as planning for 100%, 75%, and 50% of the observed effect show how the planning requirement changes when the target effect is smaller than the observed estimate. Smaller effects need more participants to be detected with the same planned power under the stated assumptions. The sample-size outputs depend on the observed estimate, which itself is uncertain, so they should be read as illustrations rather than as a reliable forecast of what a future study would require.

The registry record does not report that these assumptions were used to design CONTRAIL I. They should not be interpreted as evidence that the completed study was planned with these group sizes, or as a retrospective measure of whether it had sufficient power.

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 = 0.094; treatment proportion p₁ = 0.167; average p̄ = 0.130.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4759 = 0.9328.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4731 = 0.3982.
4. n = (0.9328 + 0.3982)² / (0.0729)² = 333.2, rounded up to 334 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 <- 0.09375                          # control proportion
p1 <- 0.166666666666667                          # 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(3781414)
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 = 334 (80% power), 446 (90% power)
 75% of observed effect: n per arm = 558 (80% power), 746 (90% power)
 50% of observed effect: n per arm = 1,174 (80% power), 1,571 (90% power)
power.prop.test: 333.2 
Simulated power at n = 334 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.

13. Analyses Reported by the Sponsor

The registry record reports sponsor analyses for each CFZ533 regimen versus TAC control as non-inferiority analyses, with rate-difference estimates and 95% confidence intervals. It does not provide p-values for those analyses or identify the statistical method and non-inferiority margin. Those posted analyses are the study’s reported inferential results and should be distinguished from the simple unadjusted re-calculations.

The re-calculations use the posted participant counts and provide unadjusted risk-difference comparisons, with p-values of 0.354 for the 300 mg regimen and 0.079 for the 600 mg regimen. Their purpose is to offer a straightforward check based on summary counts. They are not a reconstruction of the sponsor’s non-inferiority procedure, and their p-values do not answer the non-inferiority question. Because the estimands and methods may differ, a difference between the posted rate-difference estimates and a simple risk-difference calculation cannot be explained from the registry record alone.

The record does not indicate a discrepancy flag. The sponsor’s posted analyses remain the relevant source for the formal analyses as reported, while the re-calculations are supplementary descriptions. The missing margin and analysis details prevent an independent determination of the non-inferiority criteria from the posted information.

14. Multiplicity, Missing Data and Analysis Populations

The study lists three secondary outcomes: mean change in estimated glomerular filtration rate from randomization to Month 12, participants with treatment-emergent adverse events, and the percentage of patients with dose interruptions and permanent discontinuation of study treatment. The registry record lists five outcome measures and two analyses, but does not report a multiplicity adjustment or explain how the primary and secondary outcomes were organized into a testing hierarchy.

Multiplicity arises when several outcomes, groups, time points, or analyses are considered. In general, conducting many statistical tests can increase the chance of at least one apparently notable result under a setting where no true effects exist. A prespecified strategy can address this issue, but the registry record does not report such a strategy. It is therefore not possible to tell from the record whether the sponsor controlled the overall type I error across analyses or treated secondary results as descriptive.

The record identifies the Full Analysis Set for the primary outcome but does not report detailed membership rules. It does not describe the handling of missing primary-outcome information, withdrawals, or incomplete follow-up. Nor does it report imputation methods, sensitivity analyses, or assumptions about participants with missing data. These details matter because a composite outcome can be classified only when the relevant event status is known or handled under a stated method.

The sponsor analyses are labeled non-inferiority, but the non-inferiority margin and analysis population details beyond the primary Full Analysis Set are not reported. The statistical method, interim analyses, and the protocol’s original statistical analysis plan are also not reported in the registry record. Without these elements, readers cannot fully assess the role of multiplicity, the robustness of missing-data handling, or whether the posted inferential approach followed a prespecified plan.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pyrexia (10.6%), transplant rejection (8.3%), covid-19 (8.3%), hepatic enzyme increased (6.4%), ascites (6.2%).

The registry record reports on-treatment serious adverse events for 30 of 48 participants in the CFZ533 300 mg group, 29 of 47 in the CFZ533 600 mg group, and 20 of 32 in TAC control. The corresponding counts for participants with other adverse events are 45 of 48, 42 of 47, and 30 of 32. These are participant counts in the listed safety groups and are distinct from the primary composite outcome.

The record also lists deaths during on-treatment observation: 1 in the 300 mg group, 3 in the 600 mg group, and 0 in TAC control. In the post-treatment listing, the record reports 1 death for the 600 mg group and 0 for the other listed groups; the post-treatment adverse-event risk-set counts are zero. These listings should be read separately, rather than combined into a new total.

Among the listed serious adverse event terms, the record reports pyrexia at 10.6%, transplant rejection at 8.3%, COVID-19 at 8.3%, hepatic enzyme increased at 6.4%, ascites at 6.2%, and cytomegalovirus infection at 6.2%. The registry record does not provide enough detail to determine event duration, severity beyond the serious classification, or causal attribution. These figures describe the posted safety data and do not establish whether an event was caused by a study treatment.

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

The primary result is a comparison of participants with a composite event during baseline to Month 12. The posted counts are 8 of 48 for CFZ533 300 mg, 12 of 48 for CFZ533 600 mg, and 3 of 32 for TAC control. The endpoint combines BPAR, graft loss, and death, so it does not identify which component explains the overall group counts. Separate component counts are not reported in the registry record.

The sponsor’s analyses are labeled non-inferiority and include 95% confidence intervals. A non-inferiority interpretation depends on the margin and analysis rules chosen for the study. Since those details are not reported, the posted label and estimates cannot be independently evaluated against the formal criterion from the registry record alone. The simple unadjusted re-calculations offer a separate comparison based on the event counts; they do not replace the sponsor’s analyses or provide a test of non-inferiority.

These results should not be read as proof that one regimen is superior, equivalent, or inferior to another. An observed difference is not by itself a definitive treatment effect, particularly when the group sizes and event counts are limited and the uncertainty intervals are broad. The data describe this study’s enrolled and analyzed groups, not every possible transplant population or clinical setting.

The study was terminated, but the reason for termination is not reported in the registry record. The status alone does not explain why the study ended or how termination affected follow-up and outcome collection. Further information on missing data and analysis procedures is also not reported. The careful conclusion is therefore limited to the posted counts, sponsor analysis labels, and uncertainty information, without inferring unreported reasons or outcomes.

17. Why This Trial Matters Statistically

This trial illustrates how a binary composite endpoint can simplify a comparison while obscuring which event types contribute to the result. The primary measure combines BPAR, graft loss, and death, but the posted outcome reports only the number of participants with any component. Without component-specific counts, a reader cannot determine whether the overall pattern is driven mainly by rejection, graft loss, or death.

It also shows why the statistical question matters. A non-inferiority analysis is not interchangeable with a conventional test of whether two groups differ. The sponsor analyses are labeled non-inferiority, while the simple re-calculations are unadjusted comparisons of summary counts. Because the margin and detailed method are not reported, the formal inference cannot be reconstructed from the record. This is a useful reminder that estimates need their estimand and decision rule to be interpretable.

The different group sizes and limited primary-event counts make precision central to reading the findings. Point estimates alone can conceal substantial uncertainty. Confidence intervals convey a range of compatible effects, but their relevance to non-inferiority depends on the margin. Planning illustrations based on observed effects also require caution because the observed effects are uncertain and do not establish the original study’s design assumptions.

Finally, the record highlights the importance of transparent reporting on analysis populations, missing data, multiplicity, and study termination. Those details affect how confidently readers can reproduce and interpret results. Their absence does not erase the posted findings, but it limits what can be concluded from them.

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.

Several trial-specific limitations constrain interpretation of the posted results. The study was open-label, so participants and study personnel were not masked. The record does not describe whether outcome assessors beyond the stated central pathologist evaluation for BPAR were masked. Graft loss and death were evaluated locally, according to the record.

The primary outcome is a composite, and no component-specific event counts are reported. The primary analysis group sizes were 48, 48, and 32, with relatively few composite events. This makes the result sensitive to the classification of a small number of participants and limits the precision of comparisons.

The registry record labels sponsor comparisons as non-inferiority analyses but does not report the non-inferiority margin, the detailed statistical method, or the decision rule. It also does not report the protocol’s original sample-size assumptions, allocation procedure details, interim analyses, or a complete statistical analysis plan. The planning illustrations therefore should not be mistaken for the study’s original design rationale.

Handling of missing outcome information and withdrawals is not reported, and component-specific sensitivity analyses are not available in the record. The study status is terminated, but the reason for termination and its implications for follow-up are not reported. These unknowns limit assessment of potential effects on the analysis and prevent a fuller account of how the study reached its posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of Efficacy, Safety, Tolerability, Pharmacokinetic (PK) and Pharmacodynamic (PD) of an Anti-CD40 Monoclonal Antibody, CFZ533, in Liver Transplant Recipients With Additional 12-month Follow-up and Long-term Extension — NCT03781414.
• Registry record last updated 2025-05-16; status last verified 2025-05.
• Results first posted 2024-07-03.
• 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

CONTRAIL I was a Phase 2, randomized, open-label, multicenter, parallel-group study in adult de novo liver transplant recipients. It compared two CFZ533 regimens with TAC, MMF, and CS. The registry record lists enrollment of 129, a terminated status, and primary completion on 2023-04-20.

The primary endpoint counted participants with BPAR, graft loss, or death from baseline to Month 12 in the Full Analysis Set. The posted counts were 8 of 48 for CFZ533 300 mg, 12 of 48 for CFZ533 600 mg, and 3 of 32 for TAC control. Sponsor analyses are labeled non-inferiority, but the margin and detailed method are not reported. Missing-data handling, multiplicity procedures, and the reason for termination are also not reported in the registry record.