C1INH Inhibitor Preoperative and Post Kidney Transplant to Prevent DGF & IRI: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for C1INH Inhibitor Preoperative and Post Kidney Transplant to Prevent DGF & IRI (NCT02134314), a randomized phase 1, phase 2 study. The primary outcome is Number of Patients Enrolled With Serum Creatinine >3mg/dL on Postoperative Day 5..

2. Clinical Question

The clinical rationale recorded for the study links complement activation with IRI and inflammatory cell infiltrates, and proposes that blocking complement activation might affect post-transplant graft function. That rationale is the hypothesis motivating the comparison; it is not itself a result of the trial. The reported primary endpoint focuses on one early laboratory threshold. Other listed outcomes address serum creatinine, creatinine clearance, urine output, dialysis, and DGF categories, giving a broader set of measures of early kidney function.

3. Trial Design

This was a randomized, triple-masked, parallel-group phase 1/phase 2 trial. The registry record lists an enrollment of 70 and describes two groups: C1-Inhibitor (Berinert) (Human) (C1INH) and Normal Saline. Both groups were to receive standard-of-care immunosuppressive therapy in addition to their assigned study treatment. The trial status is completed. The sponsor is Cedars-Sinai Medical Center.

The study start is recorded as 2014-09, and primary completion is recorded as 2017-03-13. The registry record does not report the random-sequence method, allocation concealment procedures, or the identities of the groups of people included in the triple masking. It also does not report the intervention dose, detailed administration schedule, or criteria defining high-risk deceased donors. Those details should not be inferred from the design labels.

The primary endpoint has a timeframe of the first 7 days post-transplant and counts participants with serum creatinine above 3 mg/dL on postoperative day 5. The primary result lists 34 participants in the C1INH group and 35 in the saline group. The arm descriptions state 35 patients per group, so the recorded endpoint denominators do not match the planned arm descriptions for the C1INH group. Reasons for this difference, and the handling of missing or unavailable endpoint measurements, are not reported in the registry record.

Results are also listed for three continuous secondary measures through up to 90 days post-transplant or at 24 hours post-transplant. Additional secondary outcomes include dialysis and DGF categories. The registry record does not report the original statistical analysis plan or its sample-size justification. The trial’s completed status and reported enrollment do not establish how the original design assumptions were selected.

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

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients Enrolled With Serum Creatinine >3mg/dL on Postoperative Day 5., measured over First 7 days post-transplant.

The primary endpoint counts participants whose serum creatinine was above 3 mg/dL on postoperative day 5. Its stated timeframe is the first 7 days post-transplant. This is a binary endpoint: each participant is classified according to whether the stated threshold was met, and the result is reported as a count within each group. It is not the average creatinine concentration, nor does it describe the full trajectory of kidney function over time.

A threshold-based endpoint can make a clinically relevant laboratory status easy to compare between groups at a specified time. However, dichotomizing a continuous laboratory measurement discards information about how far a participant’s value lies above or below the cutoff. The chosen endpoint also captures one time point, so it cannot by itself describe subsequent recovery, persistent impairment, dialysis use, or other dimensions of transplant outcomes.

The posted counts are 29 of 34 in the C1INH group and 32 of 35 in the Normal Saline group. The comparison is expressed as a risk difference, with the saline group compared against C1INH. A positive difference therefore corresponds to a higher observed proportion meeting the creatinine threshold in the saline group. The estimate is uncertain, as reflected in its confidence interval, and should be read as a group-level comparison rather than a prediction about an individual participant.

Although the study rationale concerns DGF and IRI, the primary endpoint is specifically the creatinine threshold described in the registry record. It should not be treated as interchangeable with every listed DGF measure or with the study’s broader biological rationale.

7. Results Posted in the Registry

• Normal Saline: 91.4% (32/35) versus 85.3% (29/34) on control; risk difference 6.1 percentage points (95% CI -9.0 to 21.2), risk ratio 1.07 (0.90–1.27); unadjusted two-proportion z-test p = 0.426.

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.

Serum Creatinine

• 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:
  • Normal Saline: mean 1.70 versus 1.30 on control; difference 0.40 (95% CI -0.08 to 0.88), standardized effect d = 0.39; z-test p = 0.102.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Normal Saline and the control. The interval gives the range of effects that remain compatible with the data.

Creatinine Clearance

• 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:
  • Normal Saline: mean 51.20 versus 56.40 on control; difference -5.20 (95% CI -12.98 to 2.58), standardized effect d = -0.32; z-test p = 0.190.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Normal Saline and the control. The interval gives the range of effects that remain compatible with the data.

24h Urine Output

• 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:
  • Normal Saline: mean 607.80 versus 873.50 on control; difference -265.70 (95% CI -756.22 to 224.82), standardized effect d = -0.25; z-test p = 0.288.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Normal Saline and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related but distinct aspects of post-transplant kidney function: serum creatinine, creatinine clearance, 24-hour urine output, dialysis, and DGF categories. Numerical continuous summaries are available for serum creatinine, creatinine clearance, and urine output. Those outcomes use different units and timeframes, and their contrasts do not all point in the same direction. Their confidence intervals include zero, so the posted estimates do not provide precise evidence about the size or direction of each group difference.

These results offer context for the primary creatinine-threshold comparison, but they measure different features. A continuous serum creatinine average is not equivalent to the number of participants above a threshold at postoperative day 5. Creatinine clearance and urine output also characterize kidney function differently, and the timing of measurement differs. Results from these outcomes may be informative when considered together, but they should not be collapsed into one overall treatment effect without a prespecified method for doing so.

Although dialysis and DGF categories appear among the listed secondary outcomes, numerical group comparisons for those measures are not included in the posted secondary results described in the registry record. The absence of a posted summary does not establish what the underlying observations were or why a result is not presented.

Secondary results generally carry less weight than a clearly prespecified primary comparison because they may be more exploratory, and because examining multiple outcomes raises the possibility of chance findings. The registry record does not report a multiplicity strategy, a hierarchy among secondary outcomes, or sponsor-reported secondary analyses. Consequently, the unadjusted secondary estimates are best treated as descriptive and hypothesis-generating. They neither confirm the primary result nor independently settle the treatment question.

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

• Serum Creatinine
• Creatinine Clearance
• 24h Urine Output
• Mean Number of Patients on Dialysis
• Number of Patients With Delayed Graft Function (DGF) (Categorized by DGF Scale)

9. Statistical Interpretation

10. Statistical Methods Explained

The main comparison is between two randomized parallel groups: C1INH and Normal Saline. Randomization is intended, in general, to make treatment groups comparable on average with respect to factors that could influence outcomes. Masking is intended, in general, to reduce the influence of expectations or knowledge of treatment assignment on care, measurement, or assessment. The registry record labels the design randomized and triple masked but does not describe the procedures used to achieve those aims. Those design labels do not by themselves show how successfully bias was prevented.

What does a risk difference mean?

A risk difference compares the proportion with an event in one group with the proportion in another. For this endpoint, the event is meeting the serum creatinine threshold on postoperative day 5. The reported comparison is oriented as Normal Saline minus C1INH. Its estimate of 0.061 represents the difference on the risk scale, with a positive value indicating a larger observed proportion in the saline group. The risk difference keeps the comparison on the scale of the endpoint proportions; it does not express a relative change.

The posted comparison also gives a confidence interval and an unadjusted p-value. A confidence interval describes a range of values for the group difference that are reasonably compatible with the data under the statistical method’s assumptions. It reflects sampling uncertainty, not uncertainty about every possible source of bias or measurement error. A p-value summarizes the compatibility of the data with a specified null comparison, conditional on the model and assumptions. Neither statistic alone establishes clinical importance or proves that the groups are identical.

How should continuous outcomes be read?

The secondary serum creatinine, creatinine clearance, and 24-hour urine output outcomes are reported as means with standard deviations. A mean describes the average observed value in a group. A standard deviation describes the spread of participant measurements around that mean; it is not the uncertainty in the mean and is not a confidence interval. The comparison for each continuous outcome is a mean difference, with the stated contrast oriented as saline minus C1INH. Positive and negative signs therefore need to be interpreted in relation to that ordering and to the outcome’s units.

The difference between group means is a summary of the observed contrast, but individual values may vary considerably within each group. A confidence interval for a mean difference conveys uncertainty in the estimated contrast. If it includes zero, the data are compatible with no mean difference as well as with values on either side of zero. This does not mean that the group means are proven equal. The standard deviations for 24-hour urine output are large relative to the means, signaling considerable dispersion in the reported observations. In general, substantial variability can make a group mean less precise and can make a difference harder to estimate reliably.

What does unadjusted mean?

The reported p-values are unadjusted. In general, an unadjusted comparison evaluates an outcome without accounting for the fact that other outcomes may also have been examined. When many outcomes or analyses are considered, the chance of at least one apparently notable result can increase. Methods such as prespecified outcome hierarchies or multiplicity adjustments can address aspects of this issue, but the registry record does not report whether such methods were planned or used. The posted estimates should not be read as if a correction had been applied.

The registry record lists 13 outcome measures and identifies secondary outcomes that include laboratory measurements, urine output, dialysis, and DGF categories. It reports no secondary analyses. Numerical comparisons for the continuous secondary results are unadjusted recalculations from the posted summary statistics. The registry record does not provide a detailed analysis population definition, a model specification for the sponsor’s original analysis, or a description of how missing observations were handled.

What can the reported numbers establish?

These statistics describe observed group summaries and uncertainty around selected contrasts. They do not establish the biological pathway through which an outcome might change, and they do not identify why a participant’s outcome occurred. Randomized allocation supports a causal comparison when the trial conduct, follow-up, and analysis preserve the randomized comparison, but the registry record does not provide enough detail to assess all of those conditions. In general, departures from assigned treatment, missing outcomes, or post-randomization exclusions can complicate interpretation; whether any occurred and how they were handled are not reported in the registry record.

The results are also limited by the precision available from the posted group data. A point estimate is only one estimate of a group contrast, while its confidence interval expresses uncertainty under the method used. A wide interval can include effects in opposing directions, which makes a strong conclusion unwarranted. Conversely, an unremarkable p-value does not establish that a potentially important effect has been excluded. The meaningful interpretation combines the endpoint definition, direction of the contrast, effect estimate, interval, and study conduct information rather than relying on a single statistic.

11. Confidence Intervals and Precision

Precision concerns how narrowly an effect is estimated. The primary risk-difference estimate is 0.061, with a confidence interval from -0.090 to 0.212. Because the interval includes zero and extends to both negative and positive values, the primary result does not pin down the direction of the group contrast. The observed point estimate favors a higher event proportion in the saline group, but the interval also allows a lower proportion in that group. The estimate should therefore be interpreted with its uncertainty rather than as a fixed value.

The continuous-outcome intervals also include zero: -0.079 to 0.879 for serum creatinine, -12.98 to 2.579 for creatinine clearance, and -756.2 to 224.8 for 24-hour urine output. Their widths indicate that the estimated contrasts retain uncertainty. The endpoints use different units and scales, so interval widths cannot be compared directly across outcomes. Precision is best judged in relation to each outcome’s scale and to the range of effects that would matter for the scientific question. Such a clinically important range is not reported in the registry record.

A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it account for every limitation of study design and reporting. It is a statistical interval based on a method and its assumptions. The registry record does not state the method used for the original sponsor analysis of the primary outcome. The displayed comparisons are unadjusted recalculations from posted summary statistics, and the record does not list sponsor-reported secondary analyses. There is no reported discrepancy between the posted summaries and these recalculations.

The intervals are not evidence of equivalence. Demonstrating equivalence or excluding effects of a particular size requires a suitable design and a prespecified margin, which are not reported in the registry record. The appropriate reading is that the point estimates have limited precision, with plausible values spanning materially different directions or magnitudes. This statistical uncertainty is separate from questions about clinical importance and from possible bias or missing data.

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 illustrations give participants per arm for 80% power and participants per arm for 90% power. They are not totals across both groups and are not total event counts. In general, power is the chance that a planned analysis will detect an effect of a specified size under the planning assumptions, if that effect is truly present. The 80% and 90% columns therefore describe different target chances of detecting the selected effect; the higher target generally requires more participants under otherwise comparable assumptions.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. Rows planning for 100% of the observed effect use the full observed estimate; rows planning for 75% or 50% use smaller effects. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under these assumptions. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

These figures are retrospective planning illustrations based on the observed estimates, not the trial’s enrollment target or its original power calculation. They are not observed power. Observed power calculated after a trial from its estimated effect does not add a useful independent summary of the result; the estimate and its confidence interval communicate the observed uncertainty more directly. Planning figures can instead help illustrate how much larger a future study might need to be under the stated assumptions, while recognizing that the observed effect is itself uncertain and may not be the true effect.

For the continuous outcomes, the planning illustrations are based on the posted mean differences and variability. For the primary binary outcome, they relate to the difference in event proportions. Each outcome has its own effect scale and planning values, so the figures should be read within the outcome to which they apply rather than compared as if they measured a common quantity.

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 = 0.853; treatment proportion p₁ = 0.914; average p̄ = 0.884.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4535 = 0.8889.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4514 = 0.3799.
4. n = (0.8889 + 0.3799)² / (0.0613)² = 427.8, rounded up to 428 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 <- 0.852941176470588                          # control proportion
p1 <- 0.914285714285714                          # 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(2134314)
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 = 428 (80% power), 573 (90% power)
 75% of observed effect: n per arm = 805 (80% power), 1,077 (90% power)
 50% of observed effect: n per arm = 1,908 (80% power), 2,553 (90% power)
power.prop.test: 427.8 
Simulated power at n = 428 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.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists 13 outcome measures, including the primary endpoint and secondary measures covering laboratory values, urine output, dialysis, and DGF categories. It does not report a statistical analysis plan that specifies how these outcomes were prioritized or how repeated testing was addressed. No multiplicity adjustment is described in the registry record. The posted p-values should therefore be understood as unadjusted comparisons, not as values adjusted for the number of outcomes or analyses.

In general, examining multiple outcomes can increase the chance that at least one result appears notable by chance. This does not make every secondary finding invalid, but it makes prespecification and transparent reporting important. The registry record does not report whether a hierarchy, family-wise error procedure, false-discovery approach, or other strategy was used. No such method should be assumed.

The registry record does not report the original sample-size justification, interim analyses, analysis populations, or the sponsor’s full statistical analysis plan. It also does not describe an intention-to-treat analysis, a per-protocol analysis, or any other population definition. For the primary outcome, the posted denominators are 34 in the C1INH group and 35 in the saline group, while the arm descriptions state 35 patients per group. The reason for the difference and its relationship to missing data are not reported in the registry record.

Missing-data methods, outcome ascertainment rates, imputation procedures, and sensitivity analyses are not reported. The registry record also does not explain whether participants who stopped treatment or deviated from assigned treatment remained in the analysis. These omissions limit assessment of how closely the reported comparisons preserve the randomized groups and whether missing measurements could have affected the estimates. They do not prove that missing data or deviations occurred; they mean the relevant handling details are not reported in the registry record.

The registry record provides no detailed sponsor-reported secondary analyses. The numerical secondary comparisons are unadjusted recalculations from the posted group summaries. Thus, the secondary findings should be interpreted cautiously, and the absence of analysis details should remain distinct from evidence that any particular analysis procedure was or was not used.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abdominal pain (5.7%), bacteremia (2.9%), neutropenia/fever (2.9%), viral infection (2.9%), purulent drainage from wound (2.9%).

The registry record reports serious adverse events in 10 of 35 participants at risk in the C1INH group and 10 of 35 participants at risk in the Normal Saline group. Other adverse events are reported for 28 of 35 participants at risk in the C1INH group and 26 of 35 at risk in the saline group. Deaths are reported as 0 in each group. These counts describe the safety entries posted in the registry record; they do not by themselves establish whether an event was caused by study treatment.

The listed serious adverse-event terms include Abdominal pain at 5.7%, and Bacteremia, Neutropenia/Fever, Viral infection, Purulent Drainage from wound, and Acute Encephalopathy at 2.9% each. The registry record does not provide enough detail in these entries to infer a comparative risk for each term or to determine whether events could overlap within participants. The percentages should be read as reported, not recalculated or combined.

Safety comparisons require attention to definitions, follow-up duration, event ascertainment, and exposure. The available entries do not describe those details fully, nor do they provide a statistical comparison of adverse-event rates. Counts from a trial of this size and design should be treated as descriptive. They do not establish that the groups have equal safety profiles, and they do not prove that any listed event was related to the intervention.

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

The primary result describes an observed difference in the proportion of participants whose serum creatinine exceeded 3 mg/dL on postoperative day 5. The point estimate is higher for the saline group than for the C1INH group, but its confidence interval includes zero and extends to differences in either direction. The result is therefore uncertain about both the direction and size of the underlying group contrast. It does not establish that the treatments have the same effect, nor does it establish a definitive difference.

The endpoint is a specific laboratory threshold measured at a specific postoperative time. It is not a comprehensive measure of graft function, all forms of DGF, IRI, or long-term outcomes. Secondary measures offer additional descriptions, but their differing timeframes, units, and definitions mean they do not combine automatically into one overall conclusion. Some listed secondary outcomes lack numerical summaries in the registry record, and the posted secondary comparisons are unadjusted.

The study’s rationale describes a possible connection between complement activation, ischemic reperfusion injury, and graft function. The posted outcome summaries do not directly measure whether that biological pathway was changed, and they cannot by themselves establish a mechanism. Likewise, group-level estimates do not predict an individual recipient’s outcome. The registry record does not provide enough detail about missing data, analysis populations, or the original statistical plan to resolve every concern about the conduct and analysis of the trial.

The appropriate conclusion is limited to what the record reports: observed primary and secondary group summaries, with intervals that leave meaningful uncertainty. A nonsignificant p-value is not proof of no effect, while a point estimate alone is not proof of a real effect. The posted results should be read alongside the endpoint definitions, confidence intervals, safety counts, and reporting limitations. They do not amount to medical advice or a determination about which treatment should be used.

17. Why This Trial Matters Statistically

This trial raises statistical issues that are common in small randomized studies of complex clinical outcomes. The primary endpoint is a binary threshold derived from a laboratory measure, while the secondary outcomes include continuous laboratory values, urine output, dialysis, and DGF categories. These outcomes offer different views of early graft function, but their differences in definition and timing complicate any attempt to summarize them as one result.

The primary estimate illustrates why uncertainty matters alongside direction. The observed risk difference is positive for the saline-minus-C1INH contrast, yet its confidence interval includes zero and values on either side. A reader who focuses only on the point estimate could overstate what the data establish; a reader who focuses only on the p-value could wrongly treat a nonsignificant result as evidence of equivalence. Interpreting the estimate and interval together is more informative.

The registry record also makes clear the distinction between the trial’s reported enrollment and the analysis denominators for the primary endpoint. The C1INH group’s endpoint denominator is 34, whereas the arm description states 35 patients. Without information about missing outcomes or analysis populations, readers cannot determine the reason for that discrepancy. Transparent reporting of participant flow and missing-data handling is important for judging how well an analysis reflects randomized assignment.

Finally, the planning illustrations show how sample-size needs depend on the effect size targeted and the assumptions chosen. They are not evidence that the completed trial had a particular observed power. The original design justification is not reported in the registry record. Together, these features make the study a useful example of reading estimates, precision, multiplicity, and reporting completeness as separate but related parts of statistical interpretation.

18. Limitations

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

The registry record does not report several details needed to assess the trial’s execution and analysis fully. These include the eligibility criteria used to identify high-risk deceased donors, the treatment dose and schedule, the randomization procedure, allocation concealment, and which parties were included in triple masking. The record identifies the design labels but does not describe how these procedures were implemented.

The primary endpoint denominator is 34 for C1INH and 35 for Normal Saline, although each arm description states 35 patients. The reason for that difference is not reported in the registry record. There is no posted participant-flow account, missing-data method, or sensitivity analysis to show how unavailable measurements were addressed. The analysis population and handling of deviations from assigned treatment are also not reported.

The statistical analysis plan, original sample-size justification, and any interim analyses are not reported in the registry record. The registry lists 13 outcome measures, but no multiplicity strategy is described. Secondary numerical results are unadjusted recalculations from posted summaries, and sponsor-reported secondary analyses are not listed. These limits make it difficult to assess whether outcome selection, analysis choices, or incomplete reporting could affect interpretation.

The primary result concerns an early threshold-based laboratory endpoint, while longer-term or broader clinical outcomes are not established by that measure. Several secondary outcomes are listed, but numerical results for dialysis and DGF categories are not included in the posted secondary summaries. The safety entries are descriptive and do not include comparative statistical analyses or enough detail to attribute events to treatment. These reporting limitations do not demonstrate that problems occurred; they identify information not reported in the registry record that would be needed for a fuller assessment.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: C1INH Inhibitor Preoperative and Post Kidney Transplant to Prevent DGF & IRI — NCT02134314.
• Registry record last updated 2018-06-25; status last verified 2018-06.
• Results first posted 2018-06-25.
• 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

NCT02134314 is a completed randomized, triple-masked, parallel-group phase 1/phase 2 trial sponsored by Cedars-Sinai Medical Center. It compared C1 esterase inhibitor (Berinert) plus standard-of-care immunosuppressive therapy with Normal Saline placebo plus standard-of-care immunosuppressive therapy in recipients of deceased-donor kidneys from high-risk donors. The registry record lists enrollment of 70, a start of 2014-09, and primary completion on 2017-03-13.

The primary endpoint counted participants with serum creatinine above 3 mg/dL on postoperative day 5. The posted comparison has an unadjusted risk difference of 0.061 for saline minus C1INH, with a confidence interval from -0.090 to 0.212 and an unadjusted p-value of 0.426. The interval includes zero and indicates substantial uncertainty about the direction and size of the contrast.

Secondary summaries cover serum creatinine, creatinine clearance, and 24-hour urine output; additional listed outcomes concern dialysis and DGF categories. Serious adverse events are reported for 10 of 35 participants at risk in each group, with 0 deaths in each group. The registry record does not report the original statistical analysis plan, sample-size justification, missing-data methods, or multiplicity strategy.