Pilot Study of Reparixin for Early Allograft Dysfunction Prevention in Liver Transplantation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pilot Study of Reparixin for Early Allograft Dysfunction Prevention in Liver Transplantation (NCT03031470), a randomized phase 2 study. The primary outcome is Incidence of EAD (Early Allograft Dysfunction) Within 7 Days After OLT (PP Population).

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, parallel-group, open-label pilot clinical study sponsored by Dompé Farmaceutici S.p.A. The registry record lists enrollment of 40 and describes the study population as patients undergoing orthotopic liver transplantation. Participants were assigned to Reparixin or control. The control group did not receive study therapy, while both groups received standard immunosuppressive therapy.

Reparixin was given as a continuous intravenous infusion at 2.772 mg/kg/hour for 7 days. The primary endpoint assessed EAD within 7 days after OLT in the per-protocol population. The record also lists secondary outcomes covering allograft dysfunction, primary allograft nonfunction, laboratory findings, donor-organ characteristics, creatinine clearance, and mortality. The registry lists 22 outcome measures and 9 analyses.

The study status is terminated. The primary endpoint description says that 5 out of 22 patients in the Reparixin group experienced EAD during the first stage of the study and that, according to the protocol and the Data Monitoring Committee conclusion, early termination was decided. The original stopping criteria, the planned enrollment for the study, and the timing or details of any interim analyses are not reported in the registry record. The record's enrollment figure should therefore not be interpreted as evidence that the originally intended enrollment was completed.

The primary analysis population was per protocol, whereas several posted secondary outcomes use a modified intention-to-treat population. This distinction matters: the groups represented in the primary and secondary endpoint analyses are not identical. The full details of the analysis populations and the handling of patients excluded from each analysis are 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 admitted to the transplant center immediately before OLT surgery who signed the Patient Informed Consent Form underwent screening procedures (Day -1). Screening can be carried out within 24 hours before planned surgery. The results at screening were considered as baseline values. During the screening physical examination, patients fulfilling all the inclusion criteria and none of the exclusion criteria were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per protocol population (PP) includes all patients who have received at least 70% of the dose of the study drug, with data sufficient for the primary efficacy analysis, and who are considered compliant. Patients are considered compliant in case of absence of any major protocol violations during the study. In the group of the study therapy the patients who received not less than 70% of the study drug dose will be considered compliant.

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: Modified population of patients who received treatment (mITT = modified intent-to-treat) corresponds to all patients who received any dose of study drug. Two patients in the SoC arm didn't, so demographic characteristics of patients are listed for this population (n=22 in the Reparixin group and n=16 in the SoC group, for a total of n=38 patients instead of 40).

6. Primary Endpoint

The registry lists the primary outcome as Incidence of EAD (Early Allograft Dysfunction) Within 7 Days After OLT (PP Population), measured over within 7 day after the OLT.

The primary endpoint was the percentage of participants with EAD within 7 days after OLT, assessed in the per-protocol population. EAD was defined by meeting at least one of the registry's listed criteria: maximum ALT or AST levels on days 1–7 greater than 2000 U/L, a day 7 bilirubin level at least 10 mg/dl, or a day 7 international normalized ratio at least 1.6. These criteria use laboratory measures of liver injury and function to classify early dysfunction after transplantation.

A binary endpoint such as EAD records whether each participant met the definition, rather than the degree or duration of dysfunction. This makes it possible to compare the frequency of the defined event between groups. It also means that results depend on the specified thresholds and assessment window: a participant meeting any listed criterion counts as having EAD, while the endpoint does not by itself describe clinical severity, cause, or later course.

The endpoint is relevant to the study objective because the registry describes prevention of early allograft dysfunction as the central question for Reparixin. The record also identifies broader indicators of graft dysfunction during the early postoperative period, but those are not interchangeable with the prespecified primary measure. The registry record does not report a rationale for choosing this endpoint over other possible measures or a sample-size justification tied to it.

7. Results Posted in the Registry

• Reparixin - PP: 29.4% (5/17) versus 18.8% (3/16) on control; risk difference 10.7 percentage points (95% CI -18.2 to 39.6), risk ratio 1.57 (0.45–5.52); unadjusted two-proportion z-test p = 0.475.

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.

Incidence of Early Allograft Dysfunction (EAD) in Transplant Recipients With Liver Diseases of Different Etiology and With Different Baseline Characteristics

• 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:
  • Reparixin - mITT: 22.7% (5/22) versus 18.8% (3/16) on control; risk difference 4.0 percentage points (95% CI -22.0 to 29.9), risk ratio 1.21 (0.34–4.35); unadjusted two-proportion z-test p = 0.767.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Reparixin - mITT and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Early Allograft Dysfunction in Transplant Recipients (Creatinine Clearance, ClCr)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Reparixin - mITT: mean 81.60 versus 73.50 on control; difference 8.10 (95% CI -7.84 to 24.04), standardized effect d = 0.31; z-test p = 0.319.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Reparixin - mITT and the control. The interval gives the range of effects that remain compatible with the data.

Mortality Within 1 Year After the OLT

• 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:
  • Reparixin - mITT: 18.2% (4/22) versus 6.2% (1/16) on control; risk difference 11.9 percentage points (95% CI -8.1 to 31.9), risk ratio 2.91 (0.36–23.63); unadjusted two-proportion z-test p = 0.283.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Reparixin - mITT and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the study's description of early transplant outcomes beyond the primary EAD comparison. They include other indicators of allograft dysfunction, laboratory findings, donor-organ characteristics, creatinine clearance, and mortality. The posted results include both binary event measures and a continuous measure, and they use more than one analysis population. These differences mean the outcomes do not all address the same question or estimate the same quantity.

At a broad level, the posted secondary comparisons do not provide a consistent, precise basis for resolving the primary question. The EAD-related secondary analysis and mortality comparison have estimates in the direction of higher event occurrence in the Reparixin group, while the creatinine-clearance comparison has a higher reported mean in that group. The intervals are broad, and the registry record does not report confirmatory analyses for these secondary outcomes. These patterns should be considered descriptive context, not independent proof for or against the primary result.

Secondary results carry less weight when many endpoints are assessed and no multiplicity adjustment is reported. Looking across numerous outcomes creates more opportunities for chance findings, while small groups and few events make estimates unstable. The registry lists 22 outcome measures, 9 analyses, and 20 posted secondary outcomes. The record does not state that all were prespecified as confirmatory, or describe a hierarchy for interpreting them. Therefore, the secondary findings are best treated as exploratory and should not be used selectively to make a definitive claim.

The primary endpoint remains the central comparison because it directly addresses EAD within 7 days in the per-protocol population. Secondary outcomes can help characterize other aspects of the postoperative period, but they use differing definitions and timeframes and do not erase the primary estimate's uncertainty. A larger study with a reported analysis plan would be needed to establish whether any observed secondary patterns are reproducible.

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

• Number of Patients With/Without Primary Allograft Nonfunction Within 7 Days After OLT
• Number of Patients With/Without Overall Indicators of Allograft Dysfunction During the Early Postoperative Period
• Overall Indicators of the Allograft Dysfunction During the Early Postoperative Period - Extracorporeal Detoxification
• Frequency of Identification of Laboratory Examination Values
• Number of Patients With Early Allograft Dysfunction (EAD) in Case of Transplantation of Donor Organs, by the Degree of Steatosis
• Number of Patients With EAD in Case of Transplantation of Donor Organs Differing by the Time (in Hours) of Allograft Removal From the Donor and up to Its Reperfusion (Duration of Cold Ischemia)
• Number of Patients With EAD in Case of Transplantation of Donor Organs Differing by the Duration (in Min) of Warm Ischemia
• Number of Patients With EAD in Transplantation From Donors Having Additional Adverse Factors

9. Statistical Interpretation

10. Statistical Methods Explained

A two-group randomized comparison assigns participants to study groups by chance. Randomization is intended to reduce systematic differences in prognostic characteristics at assignment, but it does not guarantee balance in a small study. The study was open-label, meaning masking was not used. The registry record does not report whether outcome assessment was masked or describe methods used to address possible effects of open-label conduct.

The primary endpoint is binary: a participant either met the EAD definition within the assessment window or did not. A group percentage expresses the observed frequency of participants meeting that definition. The percentage is a descriptive estimate, not a guarantee of the event rate that would be observed in another sample. The primary analysis is explicitly identified as per protocol; its population criteria exclude participants who do not satisfy the specified dose, data, and compliance conditions. Such exclusions can affect how closely the analyzed group reflects all randomized participants. The full participant flow and reasons for exclusion are not reported in the registry record.

The registry reports a Fisher Exact analysis for the primary comparison. General explanation: Fisher's exact test evaluates evidence of association in a two-by-two arrangement of event and non-event counts across groups. It is useful when counts are small because its calculation is based on the discrete distribution of possible tables under the null hypothesis. Its p-value measures how compatible the observed table is with that null model; it is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

The recalculated contrast is a risk difference: the event proportion in one group minus the event proportion in the comparator group, using the posted summary counts. General explanation: a risk difference is an absolute contrast on the event-probability scale. A value of zero represents equal observed proportions, while values on either side represent different directions of contrast. The recalculated confidence interval quantifies uncertainty in that contrast under the stated unadjusted calculation. It is not an adjusted estimate and does not supersede the analysis reported in the registry.

A confidence interval gives a range of values reasonably compatible with the data and the method's assumptions. General explanation: a confidence interval is not a range containing a fixed proportion of individual participants, nor does it assign a probability to the true effect after the data have been observed. A wide interval signals limited precision. With small numbers of events, a few observations can materially affect the estimated group percentages and their contrast.

The registry also reports secondary outcomes of different types. Counts of participants with an event are binary outcomes; creatinine clearance is reported as a mean and standard deviation, so its comparison concerns a continuous measure. General explanation: continuous outcomes retain information about the measured value rather than reducing it to whether a threshold was crossed. However, interpretation depends on the measurement, timing, and distribution. The registry record does not report a detailed analysis plan for each secondary endpoint or whether assumptions for the continuous-outcome comparisons were checked.

Multiplicity arises when several outcomes or analyses are examined. General explanation: as the number of statistical tests increases, the chance of at least one apparently unusual result under a collection of null hypotheses can increase. Adjustments can control particular error rates, but they may also change how results are interpreted. The registry lists 22 outcome measures, 9 analyses, and 20 posted secondary outcomes. A multiplicity adjustment is not reported in the registry record. Consequently, unadjusted secondary p-values, if considered, should be treated as exploratory rather than as a collection of confirmatory tests.

The analysis populations differ across outcomes. The primary endpoint is reported for the per-protocol population, while the posted EAD, creatinine clearance, and mortality results are reported for modified intention-to-treat populations. General explanation: intention-to-treat approaches aim to preserve randomized assignment in the analysis, while per-protocol analyses focus on participants meeting specified adherence or protocol criteria. A modified intention-to-treat population can use additional eligibility rules, so the exact definition matters. The full definition of the modified intention-to-treat population and the handling of missing outcome data are not reported in the registry record.

The study's early termination affects the available evidence because the results come from the trial as conducted and reported, not from a completed sample at an unknown intended target. The record describes the reason for termination in relation to first-stage EAD experience and the Data Monitoring Committee conclusion. It does not report the original statistical plan, sample-size justification, stopping boundaries, or details of any interim analysis. Those missing design details prevent a fuller assessment of how the termination decision was planned or how it may have affected estimation.

11. Confidence Intervals and Precision

The primary group estimates have wide 95% confidence intervals. For Reparixin, the reported EAD percentage is 29.4%, with an interval from 10.3% to 56.0%. For control, it is 18.8%, with an interval from 4.0% to 45.6%. Each interval spans a broad range of possible underlying event rates, reflecting limited precision in the observed groups.

The recalculated risk difference is 0.107, with a 95% confidence interval from -0.182 to 0.396. General explanation: for a difference, an interval that includes zero is compatible with no group difference under the method used. This interval also includes values on both sides of zero, so the data do not precisely determine the direction or size of the contrast. It should not be interpreted as proof that the true effect is zero.

Confidence intervals describe uncertainty about an estimate, conditional on the statistical method and its assumptions. They do not capture every source of uncertainty. For example, they do not by themselves account for possible selection effects from the per-protocol population, open-label conduct, outcome definition choices, or early termination. The registry record does not report enough detail to quantify those sources.

The secondary outcomes also have limited precision, particularly where event counts are small. Their confidence intervals and sample-size illustrations are available alongside those results, but individual estimates should not be read as definitive. Wider intervals mean a larger range of effects remains compatible with the data. In this terminated pilot study, the most defensible emphasis is the uncertainty and range of plausible effects rather than a single point estimate.

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 the binary outcomes in the sample-size table, figures are participants per arm. If a time-to-event outcome were included, its figures would be total events; the sample-size assumptions state this distinction. The curve represents the same kind of planning relationship across effect sizes and should be read as an illustration, not as an additional observed result.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect. The columns for 80% and 90% power describe planning targets: under the calculation assumptions, the larger target is intended to give a higher chance of detecting the specified effect if that effect were true. These are design probabilities, not statements about the probability that the observed finding is true.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the required group size changes if a future study aims to detect a smaller effect. Smaller effects generally require more participants to distinguish them from random variation, all else equal. The values are illustrative because they use an effect estimated from a small, terminated pilot; that observed estimate may itself be uncertain. The original trial's sample-size assumptions and justification are not reported in the registry record.

This is not observed power. It does not indicate the probability that the trial's result is correct, and it should not be used to reinterpret the primary p-value. The illustrations answer a different question: what group size a future study might need under the stated planning assumptions and chosen effect fraction.

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 = 0.188; treatment proportion p₁ = 0.294; average p̄ = 0.241.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6047 = 1.1852.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6000 = 0.5049.
4. n = (1.1852 + 0.5049)² / (0.1066)² = 251.3, rounded up to 252 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 <- 0.1875                          # control proportion
p1 <- 0.294117647058824                          # 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(3031470)
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 = 252 (80% power), 336 (90% power)
 75% of observed effect: n per arm = 431 (80% power), 576 (90% power)
 50% of observed effect: n per arm = 929 (80% power), 1,243 (90% power)
power.prop.test: 251.3 
Simulated power at n = 252 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.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary comparison as a Fisher Exact analysis with p = 0.688. The simple unadjusted recalculation from the posted summary counts gives p = 0.475, alongside a recalculated risk difference and confidence interval. These are distinct analyses, and the recalculation is not a replacement for the registry's reported analysis.

The registry record does not explain why the two p-values differ, nor does it provide enough detail to reproduce the sponsor's full analysis beyond identifying the Fisher Exact method. The recalculation is an unadjusted check based on the posted group summaries; it does not incorporate any additional analysis features that may have been used for the sponsor's result. No adjustment or alternative covariate model is specified in the recalculation.

For interpretation of what the sponsor reported, the registry's Fisher Exact result is the relevant reported analysis. The recalculated result can help readers see how a simple summary-based contrast behaves, but it should be kept separate from the sponsor's analysis. Neither p-value alone describes the magnitude, precision, or clinical importance of the result. Those questions require considering the group estimates and confidence intervals as well as the study's small analyzed groups, per-protocol population, and early termination.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes and analyses, including 22 outcome measures, 9 analyses, and 20 posted secondary outcomes. When many endpoints are assessed, the interpretation of individual findings depends partly on whether the analyses were prespecified, how outcomes were prioritized, and whether statistical testing was adjusted for multiplicity. A multiplicity strategy is not reported in the registry record.

General explanation: testing many hypotheses without adjustment can increase the chance that at least one result appears statistically notable by chance. An adjustment can address a specified family of tests, but its choice depends on the study's aims and the relationships among outcomes. Since no strategy is reported, unadjusted secondary results should not be treated as equivalent to a single confirmatory primary analysis. The primary endpoint is identified, but the registry does not report a complete testing hierarchy or how secondary analyses were intended to support it.

Missing-data handling is also not reported in the registry record. The posted population definitions distinguish per-protocol from modified intention-to-treat analyses, but the record does not fully explain which randomized participants were omitted from each outcome, why data may be missing, or how missing values were handled. Those details matter because exclusions or missing measurements can affect both the estimated event rates and how well the analysis represents the randomized groups.

The primary analysis population required adequate data and protocol compliance, including receipt of at least 70% of the study-drug dose. This can make a per-protocol analysis informative about participants meeting those requirements, but it may not preserve all the protection against selection bias associated with analysis by randomized assignment. The full compliance definition is not reported. The modified intention-to-treat population is used for several secondary outcomes, but its detailed criteria are likewise not reported.

The original statistical analysis plan, any interim-analysis procedures, and the study's stopping rules are not reported in the registry record. The record says the study was terminated early following the first-stage EAD experience in the Reparixin group and the Data Monitoring Committee conclusion. Without the prespecified monitoring and analysis details, the effect of early stopping on estimation and interpretation cannot be assessed fully.

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 4.5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ascites (9.1%), ileus spastic (6.2%), intra-abdominal haemorrhage (6.2%), small intestinal perforation (6.2%), bile duct stenosis (6.2%).

The registry reports serious adverse events for the safety population. In the Reparixin group, 16 of 22 participants were reported with a serious adverse event; in the standard-care group, 5 of 16 were reported with a serious adverse event. Other adverse events were reported for 20 of 22 in the Reparixin group and 13 of 16 in the standard-care group. Deaths were reported for 4 of 22 and 1 of 16, respectively. These are descriptive counts in the trial groups, not estimates adjusted for differences in follow-up or baseline risk.

The listed serious adverse-event terms include Ascites at 9.1%, Ileus spastic at 6.2%, Intra-abdominal haemorrhage at 6.2%, Small intestinal perforation at 6.2%, Bile duct stenosis at 6.2%, and Hepatic artery thrombosis at 6.2%. The registry record does not provide enough information alongside these terms to establish their causes or attribute them to study treatment. Adverse-event comparisons in a small, terminated study are imprecise, and the counts should not be interpreted as proof that a treatment caused or prevented an event.

Safety findings describe reported events during the study; they do not by themselves determine a treatment's overall safety profile. The record does not report detailed event timing, severity grading beyond the serious-event classification, or a comparative statistical analysis for these safety counts.

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

The results describe a small randomized pilot study of Reparixin after liver transplantation, with EAD assessed within 7 days. The observed primary percentages were higher in the Reparixin group than in control, but the confidence intervals are wide and the recalculated interval for the risk difference includes zero. The registry's reported Fisher Exact p-value also does not provide strong evidence of a group difference. These findings are uncertain and should not be reduced to a claim that the intervention either works or does not work.

A non-significant comparison does not establish that the groups are the same. The trial does not report an equivalence or non-inferiority objective or margin, and its limited precision leaves a broad range of possible effects compatible with the data. Conversely, the observed point estimates alone do not establish that Reparixin increased EAD. Random variation, the small analysis groups, population definitions, and early termination all constrain interpretation.

The primary endpoint is a threshold-based measure of early graft dysfunction. It captures whether participants met one or more specified laboratory criteria during a defined period, but it does not summarize every aspect of graft function, clinical severity, or later outcome. The secondary outcomes add different kinds of information, yet their differing timeframes, populations, and multiplicity mean that they cannot be combined into a single definitive conclusion.

The study was terminated after the first-stage experience described in the registry. This is important context, but it does not show what a fully completed study would have found. The original sample-size rationale, stopping rules, and detailed interim procedures are not reported in the registry record. Readers should therefore treat the estimates as observations from the study as conducted, not as a conclusive estimate of the effect in all transplant recipients.

The safety counts likewise describe reported events, not causal attribution. In sum, the record contributes preliminary comparative information and identifies substantial uncertainty. It does not establish the presence, absence, magnitude, or clinical importance of a treatment effect.

18. Why This Trial Matters Statistically

This study illustrates why a randomized design does not automatically produce a precise answer. Random assignment supports a comparative question, but the primary analysis groups were small, event counts were limited, and the resulting confidence intervals span a wide range. A point estimate can look definite while its uncertainty remains substantial; interpretation should focus on both.

The record also shows how analysis-population choices shape the question being answered. The primary endpoint uses a per-protocol population, while several secondary outcomes use a modified intention-to-treat population. Those estimates are not interchangeable. Understanding who contributes data to each analysis is necessary for judging whether an estimate concerns randomized participants generally or a subset meeting post-randomization criteria.

Early termination adds another layer of uncertainty. The registry identifies a termination decision connected to first-stage EAD experience and a Data Monitoring Committee conclusion, but does not report the original stopping plan or sample-size rationale. Without those design details, the available result cannot be interpreted as though it came from a completed trial with a known target.

Finally, the record includes many outcomes, yet does not report a multiplicity strategy. That makes secondary findings useful as descriptive signals, but less suitable as standalone confirmatory claims. Together, these features make the trial statistically instructive: estimates, intervals, analysis populations, stopping, and multiplicity all contribute to how much confidence a result deserves.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations are specific to this study record. First, the trial was terminated early. The registry says the decision followed the first-stage finding that 5 out of 22 patients in the Reparixin group experienced EAD and the Data Monitoring Committee conclusion. The stopping criteria and the full monitoring context are not reported, so it is not possible to assess from the record whether the stopping decision followed prespecified statistical boundaries.

Second, the primary analysis is per protocol rather than a clearly documented analysis of all randomized participants. Eligibility depended on dose received, sufficient data, and compliance. The complete compliance definition and participant flow are not reported. This limits assessment of possible selection effects and the relationship between the primary analysis and the randomized groups.

Third, the study was open-label. The registry does not report masking of outcome assessment or measures taken to limit potential assessment effects. The endpoint uses specified laboratory thresholds, but that does not resolve every possible influence on measurement, timing, or data availability.

Fourth, the registry does not report the original sample-size justification, complete statistical analysis plan, handling of missing data, interim-analysis procedures, or multiplicity adjustment. Those omissions limit evaluation of whether the reported analyses match the planned methods and how secondary results should be prioritized.

Finally, estimates from small groups can be sensitive to a small number of events, and the reported intervals are broad. The record includes safety counts but does not provide enough detail to attribute events to treatment or to fully compare the circumstances of those events. These limitations support a cautious, preliminary reading rather than a definitive conclusion.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Pilot Study of Reparixin for Early Allograft Dysfunction Prevention in Liver Transplantation — NCT03031470.
• Registry record last updated 2025-01-07; status last verified 2024-12.
• Results first posted 2024-12-11.
• 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

The registry record describes a randomized, open-label, parallel phase 2 pilot study of Reparixin for prevention of EAD after OLT. Reparixin was administered by continuous intravenous infusion for 7 days; the control group received no study therapy, and both groups received standard immunosuppressive therapy.

The primary endpoint was EAD within 7 days in the per-protocol population. The record reports group percentages and confidence intervals, a Fisher Exact analysis, selected secondary outcomes, and safety counts. It also states that the study was terminated after the first-stage EAD experience and the Data Monitoring Committee conclusion.

The estimates are imprecise, secondary findings are exploratory in the absence of a reported multiplicity strategy, and key details about the original sample-size rationale, missing data, and stopping plan are not reported in the registry record. The results are best understood as preliminary evidence from the terminated study.