Belatacept Compared to Tacrolimus in Deceased Donor Renal Transplant Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Belatacept Compared to Tacrolimus in Deceased Donor Renal Transplant Recipients (NCT02152345), a randomized phase 4 study. The primary outcome is Number of Participants With Delayed Graft Function (DGF).

2. Clinical Question

3. Trial Design

This was a completed, randomized, parallel-group Phase 4 clinical trial sponsored by Columbia University. The registry lists enrollment of 57. The primary endpoint results use denominators of 24 participants in each treatment arm; the registry record does not explain the difference between the enrollment figure and the endpoint denominators. The study was unmasked, so masking was not used according to the registry record.

The comparison was between belatacept immunosuppression and standard immunosuppression based on tacrolimus in deceased donor renal transplant recipients. Both arm descriptions include rATG, mycophenolate and methylprednisolone. The registry title and summary emphasize rapid steroid discontinuation, but the precise steroid regimen and its timing are not reported in the registry record. The listed interventions also include renal transplantation.

The primary outcome was delayed graft function, assessed up to 3 months post-transplantation. Secondary outcomes covered allograft survival, rejection episodes and estimated glomerular filtration rate (eGFR), each with a stated timeframe of up to 1 year post-transplantation. The arm descriptions refer to follow-up for kidney function and patient and graft survival up to month 36, but the posted secondary results describe the listed outcomes up to 1 year. Results beyond the posted outcome timeframes are not reported in the registry record.

The registry lists a start date of 2014-06, primary completion on 2016-12-31 and overall status as completed. Details such as the randomization method, allocation concealment, original sample-size justification and protocol-level analysis plan are not reported in the registry record. The posted endpoint counts and comparisons therefore describe the available registry results, not a complete account of every design or analysis decision.

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 called into the hospital for potential renal transplants were approached for possible participation in the study if they agreed to discuss research and were eligible per study criteria. Patients were given the option to participate or decline.

Overall Study

Reasons for not completing this period:

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 Participants With Delayed Graft Function (DGF), measured over Up to 3 months post-transplantation.

The primary endpoint was the number of participants with delayed graft function (DGF), assessed up to 3 months post-transplantation. The registry definition counted a participant as having DGF if they required hemodialysis in the first 7 days after transplantation and/or had a serum creatinine decrease of <10% during 3 consecutive days after transplantation, provided there were no other confounding factors such as obstruction or infection. NGAL was identified as a verification marker. The registry says the clinical findings and marker were used as specified in the endpoint description.

DGF is the central outcome because the trial was designed around whether the immunosuppression regimen was associated with delayed early kidney function after a deceased donor transplant. A participant count gives a direct measure of how many people in each arm met the endpoint definition; it does not, by itself, describe the duration or severity of the dysfunction. The registry does not provide additional breakdowns of the specific qualifying pathway, the timing of resolution, or the role NGAL played in classifying individual cases.

The endpoint definition also makes clear that DGF classification was not intended to rely on a single laboratory pattern in every case: early hemodialysis was an alternative qualifying criterion, and potential confounding conditions were to be considered. How those criteria were adjudicated, and whether outcome assessors were blinded, are not reported in the registry record.

7. Results Posted in the Registry

• Belatacept Immunosuppression: 50.0% (12/24) versus 62.5% (15/24) on control; risk difference -12.5 percentage points (95% CI -40.3 to 15.3), risk ratio 0.80 (0.48–1.33); unadjusted two-proportion z-test p = 0.383.

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.

Percentage of Participants With Allograft Survival

• 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:
  • Belatacept Immunosuppression: 100.0% (24/24) versus 87.5% (21/24) on control; risk difference 12.5 percentage points (95% CI -0.7 to 25.7), risk ratio 1.14 (0.98–1.33); unadjusted two-proportion z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belatacept Immunosuppression and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With an Allograft Rejection Episode

• 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:
  • Belatacept Immunosuppression: 29.2% (7/24) versus 45.8% (11/24) on control; risk difference -16.7 percentage points (95% CI -43.6 to 10.3), risk ratio 0.64 (0.30–1.36); unadjusted two-proportion z-test p = 0.233.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belatacept Immunosuppression and the control. The interval gives the range of effects that remain compatible with the data.

Estimated Glomerular Filtration Rate (eGFR)

• 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:
  • Belatacept Immunosuppression: mean 46.00 versus 41.00 on control; difference 5.00 (95% CI -2.82 to 12.82), standardized effect d = 0.36; z-test p = 0.210.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belatacept Immunosuppression and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes give a mixed set of point estimates rather than a single uniform pattern. The survival and eGFR estimates are higher in the belatacept arm, while the rejection estimate is lower in that arm. Each comparison remains uncertain: the confidence intervals include the no-difference value, and the unadjusted p-values are 0.074 for allograft survival, 0.233 for rejection and 0.21 for eGFR.

These outcomes complement the primary DGF result by describing later graft status, rejection and kidney function. They do not directly answer the same question as the primary endpoint, which focused on delayed graft function. The broad intervals and modest endpoint denominators mean that the secondary estimates are not precise enough to settle whether the observed directional pattern reflects a reliable treatment difference. They also do not overturn the uncertainty in the primary comparison.

Unadjusted secondary findings carry less weight because several outcomes are considered and the registry does not report a multiplicity plan or adjusted analyses. When multiple outcomes are tested, the chance of at least one apparently unusual result can increase even if there are no real differences. General statistical practice therefore treats unadjusted secondary comparisons as exploratory unless a prespecified hierarchy or multiplicity procedure supports stronger claims. Such a procedure is not reported in the registry record.

The endpoint-specific estimates can still be useful descriptively: they show what the posted data look like for each outcome. But the secondary results should be interpreted as supporting context, not as independent confirmation of the primary result or proof of a broader treatment effect across transplant outcomes.

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

• Percentage of Participants With Allograft Survival
• Number of Participants With an Allograft Rejection Episode
• Estimated Glomerular Filtration Rate (eGFR)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as having or not having delayed graft function under the registry definition. For a binary endpoint, the event count and the number assessed in each arm are the basic data. Here, the posted counts are 12 of 24 for belatacept and 15 of 24 for tacrolimus. A risk difference compares the event proportions by subtracting the comparator proportion from the intervention proportion. Its sign depends on the order of subtraction; the posted estimate is defined as belatacept minus tacrolimus, so a negative value points toward fewer events in the belatacept arm.

A confidence interval for a risk difference describes a range of values reasonably compatible with the observed data under the calculation's assumptions. The primary interval extends from -0.403 to 0.153. Because it includes zero, the results do not clearly distinguish a difference from no difference at the stated confidence level. The interval also extends in both directions, making clear that the point estimate alone does not capture the uncertainty.

The registry comparison also gives a risk ratio and an odds ratio for the primary outcome. A risk ratio compares the event risks between arms, while an odds ratio compares the event odds. These measures use different scales and need not have the same numerical value as a risk difference. The posted primary risk ratio is 0.8, with interval 0.482 to 1.327; the odds ratio is 0.6, with interval 0.190 to 1.895. Both intervals include the value corresponding to no relative association. These are unadjusted comparisons and should be read alongside, not as replacements for, the counts and absolute risk difference.

The unadjusted p-value for the primary comparison is 0.383. A p-value measures how unusual results at least as extreme as those observed would be under a specified null model; it is not the probability that the null hypothesis is true. The registry record does not report the method used for a sponsor-led primary analysis, and no reported analyses are listed. Thus the posted p-value and interval should not be interpreted as evidence of a prespecified adjusted model unless such a model is documented elsewhere in the registry record.

How should continuous outcomes be read?

eGFR is reported as a mean and standard deviation for each arm. The belatacept mean is 46.0 mL/min/1.73m^2 with standard deviation 15.85, and the tacrolimus mean is 41.0 mL/min/1.73m^2 with standard deviation 11.45. The unadjusted mean difference is 5.0, with a confidence interval from -2.823 to 12.82 and p = 0.21. A mean difference describes the separation between group averages, while the standard deviations describe variation among participants within each arm. The interval includes zero, so the posted data do not establish a clear difference in mean eGFR.

As a general statistical point, a mean can be sensitive to unusually high or low observations, and a standard deviation does not show the shape of the outcome distribution. The registry does not report a distributional assessment, adjusted analysis, or missing-data approach for eGFR. Those details matter when deciding whether the posted summary statistics fully represent the observed data.

Why do small samples create uncertainty?

General statistical reasoning explains that estimates from small groups tend to be less precise because each participant has substantial influence on the observed event proportion or mean. For binary outcomes, changing the classification of a participant can alter the event count, and hence the estimated risk difference. For a continuous outcome, individual measurements can affect the group mean and variability. This is why effect estimates should be considered with their confidence intervals rather than interpreted from direction alone.

The trial is randomized, which supports a comparison between assigned groups in principle, but randomization does not remove sampling uncertainty. The registry does not report the method of sequence generation, allocation concealment, adherence, crossover, or analysis population. It is therefore not possible to assess from the posted record whether all randomized participants were analyzed as assigned or how deviations from treatment were handled.

What does over-dispersion mean in general?

For outcomes counted over time or across repeated observations, over-dispersion means that variability is greater than a simple model would expect. In general, ignoring over-dispersion can make uncertainty appear smaller than it is. The posted primary endpoint is a participant-level binary count, and the registry results do not report a repeated-count model or an over-dispersion assessment. That concept is therefore general context rather than a documented feature of this analysis.

For the reported endpoint comparisons, the posted analysis summaries are unadjusted. Adjusted estimates can account for prespecified covariates or design features, but the registry record does not report such models. The simple comparisons should accordingly be described as summaries of the posted group data, not as evidence that all potential confounding or prognostic variation was controlled. Randomization helps support causal interpretation when implemented and analyzed appropriately, but the limited methodological detail in the record constrains assessment of that process.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the data. The primary risk difference is -0.125, but its confidence interval runs from -0.403 to 0.153. That interval includes no difference and also allows effects in either direction. Its breadth relative to the point estimate signals considerable uncertainty in the estimated contrast. The counts behind it are 12 DGF participants among 24 in the belatacept arm and 15 among 24 in the tacrolimus arm.

The primary risk ratio interval, 0.482 to 1.327, likewise includes the value for no relative difference. The odds ratio interval, 0.190 to 1.895, also spans the null. These intervals express uncertainty on different scales, but all reinforce that the posted primary data do not pin down the effect precisely. The p-value of 0.383 is consistent with this uncertainty; it should not be read as proof of no effect.

The secondary endpoint intervals are also broad. For allograft survival, the risk difference is 0.125 with interval -0.007 to 0.257. For rejection, it is -0.167 with interval -0.436 to 0.103. For mean eGFR, the difference is 5.0 with interval -2.823 to 12.82. Each includes its no-difference value. This does not mean all possible effects are equally likely, but it does show that the registry estimates do not provide narrow bounds on the differences.

Confidence intervals are not guarantees that the true effect lies within the interval, nor do they account automatically for every source of bias or missing data. They describe uncertainty under the analysis assumptions. With endpoint denominators of 24 per arm and no reported analysis populations or missing-data methods, precision is only one part of the interpretive limitation.

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 express required sample size as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The original design assumptions used by the trial are not reported in the registry record.

The 80% power column describes a planning scenario in which a study designed under those assumptions would have an 80% chance of detecting the specified effect at the stated significance level, if that effect were the true effect and the assumptions held. The 90% power column describes the corresponding scenario with 90% power. These are design properties for hypothetical studies, not probabilities that the trial result is correct and not evidence that an observed result had a particular power.

The rows scale the effect used for planning: 100% of the observed effect, 75% of the observed effect and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. The illustrations are based on observed effects from this trial and should be treated as planning examples, not as the trial's original sample-size justification. This is not observed power.

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 = 0.625; treatment proportion p₁ = 0.500; average p̄ = 0.562.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7016 = 1.3750.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6960 = 0.5857.
4. n = (1.3750 + 0.5857)² / (-0.1250)² = 246.1, rounded up to 247 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 <- 0.625                          # control proportion
p1 <- 0.5                          # 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(2152345)
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 = 247 (80% power), 329 (90% power)
 75% of observed effect: n per arm = 435 (80% power), 582 (90% power)
 50% of observed effect: n per arm = 969 (80% power), 1,296 (90% power)
power.prop.test: 246.1 
Simulated power at n = 247 per arm: 0.800 (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 lists three secondary outcomes in addition to the primary DGF endpoint, but a multiplicity adjustment or prespecified testing hierarchy is not reported in the registry record. When several endpoints are examined, interpreting each unadjusted p-value as if it were the sole planned test can overstate the strength of evidence. The secondary comparisons are therefore best treated as exploratory summaries unless a fuller protocol or analysis plan establishes otherwise.

Reported analyses are not listed for the primary or secondary outcomes, and the registry indicates no reported analyses. The record does not specify whether the results come from an intention-to-treat, per-protocol, modified intention-to-treat or other analysis population. It also does not report a statistical analysis plan, covariate adjustment, model diagnostics, interim analyses, stopping rules or a missing-data method. These omissions limit assessment of whether outcome definitions and analyses were established before results were known.

The registry enrollment is 57, while the posted outcome denominators are 24 in each arm. The record does not explain this difference or describe participants who may not be included in an endpoint denominator. It is not possible from the registry summaries to determine whether the difference reflects non-randomized participants, exclusions, unavailable outcomes or another reason. No assumptions about missing outcomes should be made from the counts alone.

The DGF definition mentions exclusion of other confounding factors such as obstruction or infection, and identifies NGAL as a verification marker. The adjudication process, handling of incomplete marker measurements and consistency of endpoint assessment are not reported in the registry record. For the secondary endpoints, event ascertainment and handling of censoring or missing measurements are also not described. These details could affect interpretation, especially for outcomes measured over follow-up.

Consequently, the unadjusted estimates are useful descriptions of the posted data, but the registry record does not permit a full audit of the analysis strategy, multiplicity control, analysis populations or missing-data assumptions.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: delayed graft function (62.5%), rejection (45.8%), cmv quant+ (37.5%), bk quant+ (25.0%), ebv quant+ (12.5%).

The registry reports serious adverse events in 14 of 24 participants in the belatacept group and 15 of 24 in the tacrolimus group. Other adverse events are reported for 5 of 24 and 3 of 24 participants, respectively. Death counts are 4 in the belatacept group and 1 in the tacrolimus group. These are descriptive participant counts; they are not, on their own, estimates of treatment-attributable risk or evidence that one regimen caused more events.

The listed serious-event terms include Delayed Graft Function at 62.5%, Rejection at 45.8%, CMV quant+ at 37.5%, BK quant+ at 25.0%, EBV quant+ at 12.5% and Posttransplant lymphoproliferative disease at 4.2%. These terms may overlap within participants, and the registry summary does not establish whether a participant could contribute to multiple categories. The record also does not provide event-level timing, duration, severity grading or causal attribution for these figures.

Because the groups are small and the registry does not detail the safety analysis or follow-up completeness, the counts should be read as an account of reported events rather than a definitive comparative safety assessment.

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

The posted results establish that delayed graft function was recorded in 12 participants in the belatacept arm and 15 in the tacrolimus arm, with 24 participants in each endpoint denominator. The estimated risk difference favors belatacept in direction, but its confidence interval includes no difference and extends into the opposite direction. The data therefore do not give a precise estimate of the comparative effect.

The results do not demonstrate equivalence. Showing no clear difference in an imprecise study is not the same as showing that two treatments have similar effects within a defined margin. The registry does not report an equivalence or non-inferiority margin, and the confidence interval is compatible with a range of effects. Nor do the results establish that one regimen is superior: the primary interval and p-value do not provide strong evidence for a difference.

The secondary results describe survival, rejection and eGFR through the registry's stated follow-up. Their point estimates have different directions, and their intervals include no difference. Since these comparisons are unadjusted and no multiplicity plan is reported, they should not be used to make a firm claim about a consistent effect across outcomes.

The trial is a randomized comparison, but the registry summary does not provide enough methodological detail to assess randomization procedures, analysis populations, missing outcomes, adherence or endpoint adjudication. Those limitations do not erase the posted observations; they limit the strength and scope of conclusions drawn from them.

These statistics are not medical advice and do not determine which treatment is appropriate for an individual. They describe the registry results and their uncertainty. A fuller interpretation would require protocol and analysis details not reported in the registry record, as well as consideration of other relevant evidence beyond these posted results.

17. Why This Trial Matters Statistically

This trial raises a statistically important question: whether a belatacept-based regimen is associated with a different frequency of delayed graft function than a tacrolimus-based regimen in deceased donor renal transplant recipients. The registry provides event counts and comparative estimates, making it possible to examine both the direction of the point estimate and its uncertainty rather than relying on counts alone.

The main statistical lesson is the distinction between an observed difference and a precise, conclusive result. The primary point estimate is in one direction, but the confidence interval spans no difference and possible effects in either direction. This illustrates why a non-significant result cannot be treated as proof that treatments are equivalent, particularly when endpoint denominators are limited.

The record also illustrates how secondary outcomes can add context without resolving an uncertain primary comparison. Survival, rejection and eGFR address different outcomes, and the overall pattern is not a substitute for a prespecified analysis plan. Without reported multiplicity control, the secondary comparisons remain exploratory.

Finally, the gap between enrollment and endpoint denominators, along with absent reporting on missing-data methods and analysis populations, shows why complete registry reporting matters. Counts and confidence intervals are essential, but readers also need to know who was analyzed and how outcomes were handled. The trial is informative as a registry-level statistical example, while its unreported methods and limited precision constrain the conclusions that can be drawn.

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 primary endpoint denominator is 24 participants in each arm, while registry enrollment is 57. The registry record does not explain the difference, identify the analysis population or give reasons why some enrolled participants are not represented in the endpoint denominators. This prevents a clear assessment of outcome completeness and possible selection effects.

The trial is listed as unmasked, and the registry does not report whether endpoint assessors or analysts were masked. DGF combines clinical criteria, including early hemodialysis and a specified creatinine pattern, with NGAL as a verification marker. The method for adjudicating the endpoint and addressing potential confounders is not described. Definitions and assessment procedures could influence event classification.

Important design and analysis details are not reported in the registry record, including randomization procedures, allocation concealment, the original sample-size rationale, analysis populations, adherence, missing-data handling, covariate adjustment and multiplicity control. The record also does not explain whether there were protocol deviations or provide outcome-level follow-up completeness. These gaps limit assessment of bias and the robustness of the estimates.

The primary outcome is reported through up to 3 months, while the listed secondary outcomes have timeframes up to 1 year. Although arm descriptions refer to longer follow-up, later results are not included among the posted outcomes. The registry does not provide further timing details or time-to-event analyses for the survival outcome.

Finally, the small endpoint denominators yield broad confidence intervals. The results are therefore not precise enough to rule out a range of potentially important differences, and unadjusted secondary findings add further uncertainty rather than providing definitive confirmation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Belatacept Compared to Tacrolimus in Deceased Donor Renal Transplant Recipients — NCT02152345.
• Registry record last updated 2021-02-10; status last verified 2021-01.
• Results first posted 2019-09-10.
• 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

NCT02152345 is a completed, randomized, unmasked, parallel-group Phase 4 trial sponsored by Columbia University. It compared belatacept-based immunosuppression with a tacrolimus-based regimen in deceased donor renal transplant recipients. The registry lists enrollment of 57 and a primary endpoint of delayed graft function through up to 3 months post-transplantation.

DGF was reported for 12 of 24 participants receiving belatacept and 15 of 24 receiving tacrolimus. The unadjusted risk difference was -0.125, with a 95% confidence interval from -0.403 to 0.153 and p = 0.383. The estimate is uncertain and does not establish a treatment difference or equivalence.

Posted secondary outcomes address allograft survival, rejection and eGFR up to 1 year. Their intervals include no difference, and the registry does not report a multiplicity plan or analysis methods. Safety summaries list serious and other adverse-event counts and deaths but do not establish causality. Several design, analysis-population and missing-data details are not reported in the registry record.