OCS Liver PROTECT Trial: Preserving and Assessing Donor Livers for Transplantation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for OCS Liver PROTECT Trial: Preserving and Assessing Donor Livers for Transplantation (NCT02522871), a randomized na study. The primary outcome is Participants With Early Liver Allograft Dysfunction (EAD).

2. Clinical Question

3. Trial Design

The OCS Liver PROTECT Trial was registered as an international randomized, parallel-group study with no masking. Its brief description calls it a prospective, phased-pivotal trial evaluating the OCS Liver System for preserving and assessing donor livers intended for transplantation. The registry lists enrollment of 300, a start date of 2016-01-24, primary completion on 2019-10-22, and status as completed. The listed phase is NA.

The intervention arm received the OCS Liver System; the control arm received standard of care using ice. The registry reports per-protocol and mITT groups for the primary endpoint and secondary outcomes. These analysis populations are not interchangeable: they reflect different rules about which participants are included. The registry record does not provide enough detail to reconstruct all inclusion and exclusion rules for either population.

The primary endpoint was participants with EAD or primary non-function during 7 days. Patient survival at 30 days after transplant and survival at initial hospital discharge were also posted as secondary outcomes. The latter timeframe is described as discharge, at an average of 11 days. The registry lists six outcome measures and seven analyses overall, but only two secondary outcomes are included in the posted data summarized in the registry record.

Further design details—including the original sample-size justification, allocation-concealment procedures, trial-specific statistical analysis plan, and reasons for selecting the analysis populations—are not reported in the registry record. The registry’s enrollment figure should not be treated as the analyzed denominator for every outcome: the reported analysis groups vary by endpoint, and the primary-outcome description explicitly notes missing data.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 1 subject in each arm (OCS Liver and Control) has missing data and therefore the overall number of participants analyzed is different than the number reported in the Participant Flow.

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: As Treated Population

6. Primary Endpoint

The registry lists the primary outcome as Participants With Early Liver Allograft Dysfunction (EAD), measured over 7 days.

The primary endpoint counts participants who experienced EAD or primary non-function within 7 days. EAD was defined by one or more specified criteria: AST level > 2000 IU/ml within the first 7 postoperative days; bilirubin ≥ 10 mg/dl on postoperative day 7; INR ≥ 1.6 on postoperative day 7; or primary non-functioning graft within the first 7 days. Primary non-function was defined as irreversible graft dysfunction requiring emergency liver retransplantation or death, in the absence of immunologic or surgical causes.

This is a binary, participant-level outcome: each analyzed participant either met the endpoint definition or did not. Combining laboratory thresholds with a severe graft outcome makes the measure capture several forms of early graft dysfunction. The endpoint is time-bounded, so it concerns events in the first postoperative 7 days rather than later graft function.

These features also matter when interpreting the result. The endpoint does not describe the severity or duration of each component, and a participant meeting multiple criteria is still counted as a participant with the endpoint. Component-specific results are not reported in the registry record. The registry notes that one subject in each arm had missing primary-outcome data and that the number analyzed differs from Participant Flow. The endpoint therefore needs to be read together with the stated analysis population and the sponsor’s reported analysis.

7. Results Posted in the Registry

• OCS Liver - Per Protocol: 18.0% (27/150) versus 31.2% (44/141) on control; risk difference -13.2 percentage points (95% CI -23.0 to -3.4), risk ratio 0.58 (0.38–0.88); unadjusted two-proportion z-test p = 0.009.
• OCS Liver - mITT: 17.9% (27/151) versus 31.2% (44/141) on control; risk difference -13.3 percentage points (95% CI -23.1 to -3.5), risk ratio 0.57 (0.38–0.87); unadjusted two-proportion z-test p = 0.008.
• Control - mITT: 32.4% (47/145) versus 31.2% (44/141) on control; risk difference 1.2 percentage points (95% CI -9.6 to 12.0), risk ratio 1.04 (0.74–1.46); unadjusted two-proportion z-test p = 0.826.

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.

Patient Survival at Day 30 After Transplant

• 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:
  • OCS Liver - Per-protocol: 99.3% (150/151) versus 99.3% (141/142) on control; risk difference 0.0 percentage points (95% CI -1.8 to 1.9), risk ratio 1.00 (0.98–1.02); unadjusted two-proportion z-test p = 0.965.
  • OCS Liver - mITT: 99.3% (151/152) versus 99.3% (141/142) on control; risk difference 0.0 percentage points (95% CI -1.8 to 1.9), risk ratio 1.00 (0.98–1.02); unadjusted two-proportion z-test p = 0.961.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OCS Liver - Per-protocol and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OCS Liver - mITT and the control. The interval gives the range of effects that remain compatible with the data.

Patient Survival at Initial Hospital Discharge Post Liver Transplant

• 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:
  • OCS Liver - Per-protocol: 98.7% (149/151) versus 98.6% (140/142) on control; risk difference 0.1 percentage points (95% CI -2.6 to 2.7), risk ratio 1.00 (0.97–1.03); unadjusted two-proportion z-test p = 0.951.
  • OCS Liver - mITT: 98.7% (150/152) versus 98.6% (140/142) on control; risk difference 0.1 percentage points (95% CI -2.6 to 2.7), risk ratio 1.00 (0.97–1.03); unadjusted two-proportion z-test p = 0.945.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OCS Liver - Per-protocol and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OCS Liver - mITT and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes are patient survival at 30 days after transplant and survival at initial hospital discharge. Across both time points, the observed survival counts are high in the OCS Liver and control groups, and the recalculated risk differences are close to zero. Their confidence intervals include zero, so these comparisons do not establish a difference between groups. Nor do they establish that survival is equivalent: intervals including zero allow a range of possible differences.

The broad pattern differs from the primary endpoint comparison, where the posted counts and unadjusted recalculations show fewer EAD events in the OCS Liver groups. These outcomes measure different things and cover different time windows. EAD or primary non-function within 7 days is not the same endpoint as survival at 30 days or survival to initial discharge. The secondary results therefore provide additional context, rather than a direct replication of the primary result.

The registry also reports sponsor noninferiority analyses for the survival outcomes. Those analyses are distinct from the recalculated risk differences, and the registry record does not report the noninferiority margin. The secondary analyses should not be interpreted as resolving that missing detail or as establishing a general conclusion across outcomes.

Unadjusted secondary results carry less weight because multiple outcomes and analyses can increase the chance of a seemingly notable finding when each is assessed separately. The registry record does not report whether a multiplicity procedure was used or how the secondary outcomes were prioritized in the analysis plan. Their role is best understood as supporting descriptive evidence. They cannot replace the primary analysis or provide independent confirmation without regard to multiplicity, endpoint differences, and analysis populations.

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

• Patient Survival at Day 30 After Transplant
• Patient Survival at Initial Hospital Discharge Post Liver Transplant

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

General: A risk difference subtracts the event proportion in one group from the event proportion in another. It is expressed on the proportion scale, so a negative value in a comparison arranged as OCS Liver minus control indicates fewer observed endpoint events in the OCS Liver group. The estimate describes the observed data; it is not, by itself, proof that the intervention caused the difference. For the primary per-protocol comparison, the recalculated estimate was -0.132. The corresponding mITT estimate was -0.133.

General: The risk difference is one way to express a binary outcome contrast. It is not the same as a risk ratio or odds ratio, which use different scales. The registry also posts recalculated risk-ratio and odds-ratio estimates. Those measures can provide a different numerical perspective, but their interpretation depends on the measure and its interval. No single effect measure removes the need to consider study design, analysis population, and uncertainty.

What is a confidence interval?

General: A confidence interval describes a range of effect values compatible with the data and the method used to calculate the interval. It communicates precision, not the probability that a particular treatment effect is true. A wider interval indicates less precision than a narrower interval on the same scale. If a risk-difference interval includes zero, the data are compatible with no difference as well as with values on either side of zero, within the interval and under the method’s assumptions.

For the primary recalculated risk differences, the posted intervals run from -0.230 to -0.034 for the per-protocol comparison and from -0.231 to -0.035 for the mITT comparison. These intervals do not include zero. The recalculations are simple, unadjusted comparisons of posted summary statistics; they are not the sponsor’s reported noninferiority analysis.

What is the difference between a conventional comparison and noninferiority?

General: A conventional superiority-style comparison asks whether the data support a difference between groups, often assessed relative to a null value of zero for a risk difference. A noninferiority analysis instead evaluates whether an intervention is not worse than a comparator by more than a prespecified margin. That margin is central: without it, readers cannot independently assess how much difference the trial allowed when framing noninferiority. The margin is not reported in the registry record.

The sponsor’s posted primary analyses are identified as one-sided Farrington and Manning noninferiority analyses. The method name identifies the statistical approach, but the registry record does not provide the full analysis plan or margin. Therefore, the sponsor’s reported test results should be kept distinct from the unadjusted recalculations. A p-value from one framework cannot be substituted for a result from another framework.

Why do analysis populations matter?

General: A per-protocol analysis typically focuses on participants meeting specified protocol requirements, while an mITT analysis generally applies a modified intention-to-treat definition. The exact rules vary by trial and must be stated to interpret the estimates. The registry record provides group labels and analyzed counts, but the detailed definitions and handling rules are not reported. Results can differ across populations if participants are included or excluded differently, so agreement between populations is informative but does not establish that their assumptions are equivalent.

For the primary endpoint, the registry specifically notes missing data for one subject in each arm and says the overall analyzed number differs from Participant Flow. Missing outcomes can affect estimates if the likelihood of missingness is related to the outcome or differs across groups. The registry record does not report the missing-data assumptions, imputation methods, or sensitivity analyses, so their influence cannot be assessed from the posted information.

Why can secondary comparisons be harder to interpret?

General: When many outcomes or analyses are examined, the chance of obtaining at least one apparently notable result by chance can increase if each is assessed separately without adjustment. Multiplicity procedures can address this, but the chosen approach depends on the study’s analysis plan. The registry record does not report a multiplicity adjustment. Secondary outcomes should therefore be read as supportive descriptive information rather than treated as independent confirmation of the primary analysis.

General: Statistical significance and clinical importance are different questions. A p-value summarizes how unusual the observed data would be under a specified null model and assumptions; it does not quantify the size or practical importance of an effect. Estimates and confidence intervals help describe magnitude and precision, while study context and endpoint relevance inform clinical interpretation. No treatment advice follows from these statistical summaries alone.

11. Confidence Intervals and Precision

The primary recalculated risk-difference intervals are -0.230 to -0.034 for the per-protocol analysis and -0.231 to -0.035 for the mITT analysis. Both intervals lie below zero on the risk-difference scale, but they span a range of possible magnitudes. They should not be read as exact boundaries on the true effect; they express uncertainty under the unadjusted recalculation method and its assumptions.

General: Precision concerns how tightly an estimate is determined by the data and method. An interval that covers a broad range leaves more uncertainty about the effect’s magnitude. Confidence intervals are not guarantees and do not account for every possible source of error, such as bias from missing data, limitations in outcome measurement, or differences between the analysis method and the trial’s planned approach.

The secondary survival comparisons have risk-difference intervals that include zero. For survival at 30 days, the recalculated per-protocol interval is -0.018 to 0.019 and the mITT interval is -0.018 to 0.019. For survival at initial hospital discharge, the corresponding intervals are -0.026 to 0.027 and -0.026 to 0.028. These intervals include small differences in either direction; their estimates do not establish that the groups are identical.

The sponsor’s primary analysis reports a one-sided 95% upper confidence limit of -0.049 for the per-protocol difference and -0.062 for the mITT difference. These are not two-sided intervals with both limits posted, and they belong to the sponsor’s noninferiority analysis. They should not be directly substituted for the two-sided intervals from the unadjusted recalculations. The sponsor’s analysis takes precedence over the simple recalculation when describing the trial’s own analysis.

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 planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For the binary outcomes, the figures are participants per arm, not total events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is 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 planning number of participants per arm for an 80% chance of detecting the specified effect under those assumptions, if that effect is real and the calculation model applies. The 90% power column gives the corresponding planning number for a 90% chance. These are design probabilities for hypothetical future studies, not guarantees about a particular study’s result.

The rows scaling the observed effect represent planning for 100%, 75%, or 50% of the observed effect. Smaller effects require more participants to detect under the same assumptions. For example, in the primary per-protocol planning illustration, detecting 100% of the observed effect corresponds to 166 participants per arm for 80% power and 222 participants per arm for 90% power; planning for 50% of the observed effect corresponds to 724 and 968 participants per arm, respectively. The mITT planning figures are also listed separately, because they use that comparison’s observed effect.

These figures are not observed power. They do not show the probability that the completed trial detected an effect after the results were known, and they do not replace a prespecified sample-size justification. They are conditional planning illustrations whose usefulness depends on the assumed effect and calculation assumptions.

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 = 0.312; treatment proportion p₁ = 0.180; average p̄ = 0.246.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6091 = 1.1938.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6019 = 0.5066.
4. n = (1.1938 + 0.5066)² / (-0.1321)² = 165.8, rounded up to 166 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 <- 0.312056737588652                          # control proportion
p1 <- 0.18                          # 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(2522871)
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 = 166 (80% power), 222 (90% power)
 75% of observed effect: n per arm = 309 (80% power), 413 (90% power)
 50% of observed effect: n per arm = 724 (80% power), 968 (90% power)
power.prop.test: 165.8 
Simulated power at n = 166 per arm: 0.804 (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 sponsor analyses for both primary analysis populations using a one-sided Farrington and Manning method for a difference in proportions. For the per-protocol comparison, the reported difference is -0.132, with an upper 95% confidence limit of -0.049 and p < 0.001. For the mITT comparison, the reported difference is -0.145, with an upper 95% confidence limit of -0.062 and p < 0.001. These are identified as noninferiority analyses.

The simple recalculations use posted counts and produce per-protocol and mITT risk differences of -0.132 and -0.133, with two-sided confidence intervals and unadjusted p-values. The estimates and p-values do not exactly match the sponsor’s reported results. The discrepancy flag indicates that the posted analyses differ from the recalculated comparisons. The sponsor’s own analysis takes precedence when describing the trial’s analysis.

The two approaches should not be blended. The recalculation is an unadjusted comparison from summary counts; the registry identifies the sponsor method as one-sided noninferiority testing. The registry record does not report the noninferiority margin or enough of the analysis plan to reproduce the sponsor’s method independently. Without the margin, readers cannot independently evaluate the threshold used for the noninferiority question. The sponsor’s reported outcome should therefore be presented as reported, while the recalculation remains a separate descriptive check rather than a correction.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, or analyses are assessed. General: If each comparison is judged separately without adjustment, the chance of at least one result appearing notable by chance can increase. A study may address this through a prespecified hierarchy, adjustment procedure, or other analysis strategy. The registry record does not report whether such a procedure was used for the posted outcomes and analyses.

The registry lists six outcome measures and seven analyses, while two secondary outcomes are posted in the information summarized for this trial. The primary endpoint is analyzed in per-protocol and mITT populations, and the secondary outcomes also have more than one analysis population. These multiple looks are relevant when interpreting individual p-values, especially for secondary findings. The full prespecified testing hierarchy and statistical analysis plan are not reported in the registry record.

Missing data are explicitly noted for the primary endpoint: one subject in each arm had missing data, and the number analyzed differs from Participant Flow. The posted primary counts show different denominators across the listed groups. The registry record does not report how missing observations were handled beyond the stated analysis counts, whether values were imputed, or whether sensitivity analyses assessed alternative assumptions. It is therefore not possible to judge from this record alone whether missingness could have influenced the comparisons.

Per-protocol and mITT populations provide different analysis views, but their labels alone do not specify membership rules. The registry record does not report the detailed definitions or exclusions used to create these populations. That limits assessment of potential selection effects and of how closely either analysis followed the randomized assignment. These are interpretation limits, not evidence that a particular bias occurred.

The sponsor’s noninferiority margin and original sample-size justification are also not reported. The margin is necessary to understand the sponsor’s noninferiority threshold, while the original sample-size assumptions explain the design’s intended precision and power. The planning illustrations based on observed effects do not fill either gap.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: biliary ischaemia (9.6%), biliary anastomosis complication (8.5%), post procedural bile leak (7.5%), renal failure acute (7.2%), transplant rejection (4.8%).

The registry reports serious adverse events for the OCS Liver System group and the control group. Serious adverse events affected 82 of 153 participants at risk in the OCS Liver System group and 72 of 146 at risk in the control group. The registry separately reports 9 deaths in the OCS Liver System group and 10 in the control group. These figures are descriptive counts and denominators; they are not adjusted comparisons and do not by themselves establish that one group had a higher or lower safety risk.

The most frequently listed serious adverse-event terms include biliary ischaemia (9.6%), biliary anastomosis complication (8.5%), post procedural bile leak (7.5%), renal failure acute (7.2%), transplant rejection (4.8%), and post procedural haemorrhage (4.8%). The registry reports zero for other adverse-event counts in the two groups, but the meaning of those fields is not further described in the posted record.

General: Adverse-event counts depend on definitions, observation periods, event coding, and whether participants can experience more than one event. The registry record does not provide a detailed safety analysis plan, event-level timing, severity breakdown, or adjusted comparison. These summaries should not be used alone to infer comparative safety or to make treatment decisions.

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

The posted primary results describe fewer participants meeting the EAD or primary non-function endpoint in the OCS Liver groups than in the control groups. The recalculated risk differences are negative in both the per-protocol and mITT comparisons, and their confidence intervals do not include zero. The sponsor also reports noninferiority analyses with p < 0.001. Those sponsor results use a different statistical framework from the unadjusted recalculations, and the sponsor’s own analysis takes precedence.

That statistical pattern does not by itself show why the groups differed, establish the importance of the difference for every patient or transplant setting, or determine whether the OCS Liver System should be used. The trial was randomized, but the registry record alone does not provide all details needed to assess implementation, outcome assessment, or the full planned analysis. The noninferiority margin is not reported, limiting independent appraisal of the sponsor’s stated framework.

The secondary survival comparisons show similar observed counts across groups, with risk-difference intervals that include zero. This does not prove equality or rule out meaningful differences; the intervals express uncertainty over a range of values. These outcomes are also distinct from early graft dysfunction and were reported as secondary outcomes. The registry record does not report a multiplicity adjustment, which further argues for caution in treating separate secondary tests as definitive.

General: A statistically notable result is not automatically a clinically important result, and a result that is not statistically notable is not proof of no effect. Interpretation combines the estimated magnitude, precision, study methods, endpoint meaning, and context. The posted registry data can inform that assessment but cannot replace a complete trial report or clinical judgment. No treatment recommendation follows from these summaries.

18. Why This Trial Matters Statistically

This trial raises statistical questions that are common in device studies involving randomized clinical comparisons. The primary endpoint combines several criteria into a participant-level binary outcome. That makes the comparison straightforward to express as event counts and proportions, but the composite can conceal which component accounts for the observed pattern. Component-specific primary-outcome results are not reported in the registry record.

The comparison also illustrates why the analysis framework matters. A simple risk-difference recalculation from posted counts is transparent and useful for describing the data, but it is not interchangeable with the sponsor’s one-sided noninferiority analysis. Noninferiority depends on a prespecified margin, and that margin is not reported in the registry record. The sponsor’s analysis takes precedence, while the missing margin limits independent evaluation of the noninferiority question.

Multiple analysis populations, secondary outcomes, and missing primary-outcome data add further interpretive considerations. The per-protocol and mITT primary results point in a similar direction, but their detailed definitions are not reported. The registry record notes missing data and does not state the handling method or multiplicity strategy. These omissions do not establish that the findings are invalid; they identify uncertainties readers should keep in view.

Finally, precision and planning need separate treatment. The confidence intervals describe uncertainty in the estimates, while the sample-size illustrations use observed effects and specified planning assumptions. They do not recreate the original design calculations or represent observed power. Keeping these statistical roles distinct makes the registry results easier to interpret without overstating what the record can establish.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific details needed for a full assessment are not reported in the registry record. These include eligibility criteria and baseline clinical characteristics, allocation-concealment procedures, detailed operating and preservation protocols, and the complete statistical analysis plan. Without those details, readers cannot fully evaluate how participants and donor livers were selected, how the intervention was implemented, or whether the posted analyses followed the prespecified plan.

The primary endpoint combines laboratory thresholds and primary non-function, but results for its separate components are not reported. The record also notes missing primary-outcome data for one subject in each arm and a difference between analyzed numbers and Participant Flow. The missing-data handling method and sensitivity analyses are not reported. Detailed definitions for the per-protocol and mITT populations are also absent.

The sponsor’s analyses are designated noninferiority tests, but the margin is not reported. That prevents independent appraisal of the noninferiority threshold. The registry record does not report the original sample-size justification, interim analyses, or multiplicity strategy. Planning illustrations based on the observed effects do not supply those missing design details.

The posted secondary outcomes cover survival at 30 days and at initial hospital discharge, but they do not resolve longer-term outcomes. The discharge timeframe is described as an average of 11 days; no further detail about the timing distribution is reported. Serious adverse-event summaries are provided, but the record does not give event-level timing, severity breakdowns, or adjusted comparisons. These limitations define what can be concluded from the registry record; they are not evidence that an unreported procedure or analysis was or was not conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: OCS Liver PROTECT Trial: Preserving and Assessing Donor Livers for Transplantation — NCT02522871.
• Registry record last updated 2023-06-29; status last verified 2022-01.
• Results first posted 2023-06-29.
• 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 OCS Liver PROTECT Trial is listed as a completed, international randomized, open-label, parallel-group study with enrollment of 300. It compared the OCS Liver System with standard-of-care ice for donor-liver preservation and assessment. The primary outcome was EAD or primary non-function within 7 days; secondary outcomes were patient survival at 30 days and at initial hospital discharge.

The posted primary counts and unadjusted recalculations show fewer endpoint events in the OCS Liver groups in both listed analysis populations. The sponsor reported one-sided Farrington and Manning noninferiority analyses; those results take precedence over simple recalculations, while the noninferiority margin is not reported in the registry record. The secondary survival comparisons have risk-difference intervals that include zero. Missing primary-outcome data, unspecified analysis-population rules, and unreported multiplicity and original design assumptions limit independent evaluation. The record provides useful outcome summaries, but not every detail required for a complete appraisal of the trial.