Belatacept Evaluation of Nephroprotection and Efficacy as First-line Immunosuppression (BENEFIT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Belatacept Evaluation of Nephroprotection and Efficacy as First-line Immunosuppression (BENEFIT) (NCT00256750), a randomized phase 3 study. The primary outcome is Percent of Participants Surviving With a Functioning Graft by Month 12.

2. Clinical Question

The clinical question concerns both participant survival and continued graft function. A graft counted as lost if it was lost physically or functionally. Functional loss included a sustained serum creatinine threshold, dialysis for a specified duration, or renal impairment leading to retransplantation. These criteria make the outcome broader than graft survival defined only by whether a transplant remained physically present.

The registry also describes interest in kidney function, patient survival, and safety, with secondary outcomes covering measured glomerular filtration rate, chronic allograft nephropathy, adverse events, blood pressure, laboratory abnormalities, and anti-donor antibodies. These outcomes add different perspectives, but they do not replace the primary question. The primary result is a Month 12 binary outcome: each participant either met the definition of survival with a functioning graft or did not.

3. Trial Design

BENEFIT (Belatacept Evaluation of Nephroprotection and Efficacy as First-line Immunosuppression) is recorded as a Phase 3 randomized, single-masked, parallel-group trial. The registry lists Bristol-Myers Squibb as sponsor and enrollment of 738. The study is marked completed. The recorded start is 2005-03 and primary completion is 2008-06.

Participants were assigned to cyclosporine, belatacept LI, or belatacept MI. The primary endpoint results use the intent-to-treat population described as all randomized, transplanted, and treated participants. The reported endpoint-specific group sizes are 221 for cyclosporine, 226 for belatacept LI, and 219 for belatacept MI. These endpoint denominators need not match the overall enrollment because enrollment and an outcome-specific analysis denominator describe different things.

Single masking is the masking information recorded, but who was masked and how masking was maintained are not reported in the registry record. The arm descriptions are blank, so details beyond the intervention names and the LI and MI labels are not reported in the registry record. The original allocation procedures, follow-up procedures, and trial-specific sample-size rationale are also not reported in the registry record.

The registry lists 43 outcome measures and 178 analyses. The primary outcome is survival with a functioning graft by Month 12, with a timeframe from Day 1 to Month 12. Secondary outcomes extend to Month 84 for some measures, while others are assessed at Month 12 or Month 36. The range of follow-up windows means that findings across outcomes should not be treated as if they describe the same period or the same event process.

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: 738 participants enrolled, 686 randomized. Reasons for non-randomization include 5 participants withdrew consent, 1 lost to follow-up, 34 no longer met study criteria, and 12 for other non-listed reasons. 666 participants randomized, but not transplanted. 20 not transplanted; 10, 4, 6 in the CsA, Belatacept LI, Belatacept MI, respectively.

Transplanted Pre-Treatment

Reasons for not completing this period:

Post-Transplant Treated (12 Months)

Reasons for not completing this period:

Post-Transplant Treated (24 Months)

Reasons for not completing this period:

Post-Transplant Treated (36 Months)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized, transplanted, and treated participants; intent to treat (ITT) population

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: Baseline characteristics of transplant recipients: All randomized and transplanted participants, intent to treat (ITT) population

6. Primary Endpoint

The registry lists the primary outcome as Percent of Participants Surviving With a Functioning Graft by Month 12, measured over Day 1 to Month 12.

The primary endpoint is the percentage of participants surviving with a functioning graft by Month 12, measured from Day 1 to Month 12. It combines two clinically important conditions: the participant is alive, and the transplanted kidney has not met the registry’s definition of graft loss. The outcome is therefore not simply a measure of kidney function at a single visit.

Graft loss includes physical loss, such as nephrectomy, and functional loss. Functional loss was defined using sustained serum creatinine at or above 6.0 milligrams per deciliter or 530 micromolar per liter, dialysis for at least 56 consecutive days, or impairment of renal function severe enough to lead to retransplantation. The creatinine criterion is described as sustained for at least 4 weeks or at least 56 consecutive days.

A binary endpoint is useful for comparing the proportion of participants meeting a clearly specified outcome by a fixed follow-up time. It can capture events with different clinical pathways under one prespecified definition. At the same time, it does not show when within the follow-up period an event occurred, how kidney function changed among participants who retained a functioning graft, or which component of the composite definition determined an outcome. Those questions require other outcomes and analyses. The posted primary results report the group percentages and confidence intervals, while the registry record does not report a breakdown of the primary endpoint by its component criteria.

7. Results Posted in the Registry

• Belatacept LI: 96.5% (218/226) versus 92.8% (205/221) on control; risk difference 3.7 percentage points (95% CI -0.5 to 7.9), risk ratio 1.04 (0.99–1.09); unadjusted two-proportion z-test p = 0.083.
• Belatacept MI: 95.4% (209/219) versus 92.8% (205/221) on control; risk difference 2.7 percentage points (95% CI -1.7 to 7.1), risk ratio 1.03 (0.98–1.08); unadjusted two-proportion z-test p = 0.234.

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.

Percent of Participants With Prevalence of Chronic Allograft Nephropathy (CAN) at Month 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Belatacept LI: 23.9% (54/226) versus 32.4% (71/219) on control; risk difference -8.5 percentage points (95% CI -16.9 to -0.2), risk ratio 0.74 (0.55–1.00); unadjusted two-proportion z-test p = 0.045.
  • Belatacept MI: 18.3% (40/219) versus 32.4% (71/219) on control; risk difference -14.2 percentage points (95% CI -22.2 to -6.1), risk ratio 0.56 (0.40–0.79); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Belatacept LI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Belatacept MI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent of Participants With Development of Anti-Donor HLA Positive Antibodies by Month 84

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Belatacept LI: 3.1% (7/226) versus 11.6% (25/215) on control; risk difference -8.5 percentage points (95% CI -13.4 to -3.7), risk ratio 0.27 (0.12–0.60); unadjusted two-proportion z-test p = <0.001.
  • Belatacept MI: 1.4% (3/219) versus 11.6% (25/215) on control; risk difference -10.3 percentage points (95% CI -14.8 to -5.7), risk ratio 0.12 (0.04–0.38); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Belatacept LI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Belatacept MI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent of Participants With a Decrease in Measured Glomerular Filtration Rate (mGFR) Greater Than or Equal to 10mL/Min/1.73m^2 From Month 3 to Month 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Belatacept LI: 23.4% (50/214) versus 28.2% (60/213) on control; risk difference -4.8 percentage points (95% CI -13.1 to 3.5), risk ratio 0.83 (0.60–1.15); unadjusted two-proportion z-test p = 0.256.
  • Belatacept MI: 23.0% (48/209) versus 28.2% (60/213) on control; risk difference -5.2 percentage points (95% CI -13.5 to 3.1), risk ratio 0.82 (0.59–1.13); unadjusted two-proportion z-test p = 0.221.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belatacept LI 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 Belatacept MI and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address several dimensions beyond the primary Month 12 graft-and-survival measure. They include kidney function, chronic allograft nephropathy, adverse events, blood pressure, laboratory abnormalities, and anti-donor antibodies. Their follow-up periods vary, extending to Month 84 for some outcomes, so they represent a broader and longer-term picture than the primary endpoint alone.

Across the posted binary secondary results with detailed comparisons, the direction of the estimates is not uniform across all outcome types. Some outcomes have lower percentages in the belatacept groups than in the cyclosporine group, while the comparison for decline in measured glomerular filtration rate has intervals that include no difference. This range of patterns does not conflict with the primary result: secondary measures capture different events, definitions, and follow-up periods, and they need not move in parallel with survival with a functioning graft by Month 12.

Secondary analyses generally carry less weight than the primary endpoint for confirmatory interpretation, especially when many outcomes and comparisons are examined. With multiple opportunities to find a nominally unusual result, unadjusted p-values do not control the overall chance of false-positive findings across the full family of analyses. The registry lists 43 outcome measures and 178 analyses, but a multiplicity adjustment or hierarchy for interpreting those analyses is not reported in the registry record.

Secondary findings can help identify patterns that merit attention and can complement the primary result, but they should be interpreted with their own denominators, confidence intervals, and timeframes. They should not be used to make a broad claim about every aspect of kidney function or safety. The registry record does not report an integrated analysis that combines the secondary outcomes into a single overall measure.

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

• Mean Value of the Measured Glomerular Filtration Rate (mGFR)
• Percent of Participants With Prevalence of Chronic Allograft Nephropathy (CAN) at Month 12
• Number of Participants With Serious Adverse Events, Death, Discontinuation Due to Adverse Events by Month 84
• Number of Participants With Adverse Events of Special Interest by Month 84
• Mean Blood Pressure at Month 84
• Number of Participants Meeting Marked Laboratory Abnormality Criteria Post-transplant by Month 36
• Percent of Participants With Development of Anti-Donor HLA Positive Antibodies by Month 84
• Mean Change of the Measured Glomerular Filtration Rate (mGFR) From Month 3 to Month 12 and From Month 3 to Month 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either survived with a functioning graft by Month 12 or did not meet that definition. For a binary outcome, a group percentage describes the proportion of analyzed participants meeting the definition. A comparison can then be expressed as a difference between group proportions. The recalculated comparisons use the risk-difference scale and are unadjusted calculations from the posted summary statistics.

What does a confidence interval describe?

A confidence interval describes statistical uncertainty around an estimated quantity under the assumptions of the method used. For an arm-specific percentage, it gives a range of values compatible with the data and method. For a risk difference, it gives a range of plausible differences between groups. A narrower interval indicates greater precision than a wider interval, but neither interval removes uncertainty or accounts automatically for every possible source of bias.

The registry reports 95% confidence intervals for the arm percentages. The sponsor-reported primary contrasts are recorded with 97.3% confidence intervals. Those interval levels should not be treated as interchangeable: a confidence interval’s level is part of its definition. The record does not state the method used for the sponsor’s primary analysis, so that method is not reported in the registry record.

How should the p-values be read?

The recalculated p-values are unadjusted tests based on the posted summary statistics. A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The LI comparison has p = 0.083 and the MI comparison has p = 0.234. These values should be read alongside the estimates and confidence intervals rather than as standalone verdicts.

The registry’s sponsor-reported primary results do not include p-values. The reported analysis type is non-inferiority or equivalence, which asks a different question from a conventional test for any difference. A non-inferiority interpretation depends on a prespecified margin and an analysis rule. Neither is reported in the registry record. Thus, the sponsor-reported classification can be described, but the criterion cannot be independently evaluated from the registry record.

Why distinguish sponsor results from recalculations?

The recalculated statistics are simple, unadjusted calculations from posted counts and denominators. They are useful for understanding the raw group comparison, but they are not a substitute for the trial’s full analysis. The sponsor’s analysis may use a different method, population handling, or confidence-interval construction; the registry record does not report enough detail to specify those choices for the primary endpoint. The posted sponsor analysis should therefore be kept distinct from the recalculation, rather than blending their interval levels or methods.

What does the randomization contribute?

Random assignment is intended to make the treatment groups comparable on average at the start of a trial, including for factors that were not measured. This supports a causal comparison when the trial is conducted and analyzed as planned. Randomization does not guarantee that every group is identical, prevent missing outcomes, or remove uncertainty from finite data. The registry says the trial was randomized and parallel-group, but the detailed randomization procedure and the trial-specific analysis plan are not reported in the registry record.

Why does over-dispersion matter?

Over-dispersion is a general issue for count or rate outcomes when observed variability is greater than a simple statistical model expects. It can make standard errors too small if the extra variability is ignored. The primary endpoint is a binary percentage, not a count-rate endpoint, and the registry record does not report an over-dispersion adjustment for this endpoint. For other outcomes, the appropriate model depends on the outcome type and analysis plan; those model details are not reported in the registry record.

More broadly, the registry lists many outcomes and analyses. Separate unadjusted comparisons across many outcomes increase the chance that some results appear notable by chance. The registry record does not report a multiplicity strategy for the full set of analyses. Accordingly, secondary comparisons are best treated as supportive or exploratory unless their analysis and interpretation are established by a documented plan.

11. Confidence Intervals and Precision

The arm-specific confidence intervals give a sense of the precision of the Month 12 estimates. For cyclosporine, the estimate is 92.8%, with a 95% confidence interval from 89.3% to 96.2%. For belatacept LI, the estimate is 96.5%, with an interval from 94.1% to 98.9%. For belatacept MI, the estimate is 95.4%, with an interval from 92.7% to 98.2%. Each range includes uncertainty around the corresponding group percentage; it is not a range of individual participants’ outcomes.

For the recalculated group contrasts, the LI risk-difference interval runs from -0.005 to 0.079, and the MI interval runs from -0.017 to 0.071. Both span zero. Thus, the posted summary data are compatible with effects on either side of no difference under these calculations. The intervals also permit a range of possible effects, so a single point estimate should not be read as the exact underlying difference.

The sponsor-reported contrast intervals are at the 97.3% level and have different limits from the recalculated 95% intervals. This difference in interval level is important when comparing apparent precision. The sponsor’s LI interval is -1.1 to 9.0, and its MI interval is -2.5 to 8.1, for the reported difference-in-percent results. The non-inferiority margin is not reported in the registry record, preventing assessment of whether these intervals meet a particular margin-based criterion.

Precision is limited by the amount of information available for an outcome and by the number of events, not merely by the overall trial enrollment. The primary endpoint denominators are the reported endpoint group sizes, and other outcomes use their own denominators. Confidence intervals quantify sampling uncertainty under the relevant analysis; they do not account for unreported design details, outcome misclassification, or other possible systematic errors.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations are planning calculations based on the observed effect, not the original trial’s design assumptions. For these binary percentage outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to the stated fraction of the observed effect.

The 80% power column gives the planned participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect is real and the assumptions hold. The 90% power column makes the corresponding illustration for a 90% chance. Greater planned power generally requires more participants when other assumptions are held constant. Smaller effects require more participants to detect than larger effects, which is why the illustrations increase as the assumed fraction of the observed effect decreases.

These values are not observed power. They are hypothetical planning illustrations calculated after the trial from the observed effect, and they do not establish whether the trial was adequately designed for its original purpose. The registry’s original sample-size justification and design assumptions are not reported in the registry record. The calculations also depend on the observed effect, which is uncertain, so they should not be treated as a forecast of what another study would necessarily require.

The planning assumptions describe equal allocation between the two arms for each comparison. They do not describe the three-arm trial’s original allocation process. The illustrations should be interpreted as a way to understand how assumed effect size and target power relate to required per-arm enrollment, not as a recommendation or a reconstruction of the trial protocol.

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 = 0.928; treatment proportion p₁ = 0.965; average p̄ = 0.946.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3194 = 0.6259.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3183 = 0.2679.
4. n = (0.6259 + 0.2679)² / (0.0370)² = 583.5, rounded up to 584 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 <- 0.927601809954751                          # control proportion
p1 <- 0.964601769911504                          # 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(256750)
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 = 584 (80% power), 781 (90% power)
 75% of observed effect: n per arm = 1,123 (80% power), 1,502 (90% power)
 50% of observed effect: n per arm = 2,713 (80% power), 3,631 (90% power)
power.prop.test: 583.5 
Simulated power at n = 584 per arm: 0.806 (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’s sponsor-reported primary analyses compare cyclosporine with each belatacept regimen and label the results as non-inferiority or equivalence analyses. For LI, the reported difference in percent is 3.7, with a 97.3% confidence interval from -1.1 to 9.0. For MI, the reported difference in percent is 2.7, with a 97.3% confidence interval from -2.5 to 8.1. The registry does not report p-values for these primary analyses.

The recalculated comparisons use the posted counts and denominators to estimate unadjusted risk differences. Their confidence intervals are at the 95% level, and the calculations yield p = 0.083 for LI and p = 0.234 for MI. These results are related to the sponsor comparisons but are not the same analysis: they use a different calculation and interval level. They should therefore be presented separately rather than substituted for the sponsor’s reported results.

The registry record does not report the non-inferiority margin or the sponsor’s detailed primary analysis method. Without the margin and decision rule, the sponsor’s analysis classification cannot be fully assessed from the registry record. The record does not flag a discrepancy between the sponsor’s results and the recalculation. The sponsor’s own analysis remains the trial’s reported analysis; the recalculation is a descriptive, unadjusted check based on posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study makes many statistical comparisons. Even if each comparison uses a conventional threshold, testing many outcomes can increase the chance that at least one result appears statistically notable by chance. This is a general statistical concern, not evidence that any particular posted result is false. BENEFIT has 43 listed outcome measures and 178 analyses, so the context for interpreting individual secondary findings matters.

A prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory outcomes can help explain how multiple results were intended to be interpreted. Such a strategy is not reported in the registry record. The registry also does not report whether interim analyses were conducted or what stopping rules, if any, were used. These details should not be inferred from the completed status or the posted outcome results.

The primary analysis population is described as all randomized, transplanted, and treated participants in the intent-to-treat population. That description is useful, but the registry record does not give a detailed account of how missing primary outcomes were handled, whether participants with incomplete follow-up were imputed or otherwise classified, or what sensitivity analyses were performed. The outcome-specific denominators differ across measures, and reasons for those differences are not reported in the registry record.

The registry record does not report a detailed statistical analysis plan, the sponsor’s primary endpoint method, or the non-inferiority margin. It also does not report whether the planned comparisons were adjusted for baseline variables. For these reasons, the posted estimates can be described and the simple recalculations can be checked against posted summaries, but full assessment of prespecification, missing-data assumptions, and multiplicity control is not possible from the registry record alone.

These gaps do not erase the observed estimates. They define the limits of what can be concluded from the registry record: the reported results can be interpreted as results of the analyses recorded, while the unreported decisions and safeguards remain unknown.

16. Safety Results

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

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: urinary tract infection (14.9%), pneumonia (7.9%), pyrexia (7.5%), blood creatinine increased (7.4%), cytomegalovirus infection (7.3%).

The posted serious adverse event counts are 167 affected among 215 at risk for cyclosporine, 160 among 226 at risk for belatacept LI, and 164 among 219 at risk for belatacept MI. The other-adverse-event counts are 213 among 215 at risk, 222 among 226 at risk, and 216 among 219 at risk, respectively. These are counts with the recorded at-risk denominators; they are not calculated percentages, and no additional percentages are inferred.

The most frequently listed serious adverse event terms include urinary tract infection at 14.9%, pneumonia at 7.9%, pyrexia at 7.5%, blood creatinine increased at 7.4%, cytomegalovirus infection at 7.3%, and acute kidney injury at 6.0%. Those entries describe listed event terms, not a complete account of every safety outcome. The registry record does not report deaths for these groups, and the detailed timing and event-specific denominators are not reported in the registry record.

Safety counts should be read with the trial’s follow-up and event definitions in mind. They do not by themselves establish a comparative safety profile, especially without detailed information on event ascertainment, duration at risk, and analysis methods. They should also be kept distinct from the primary endpoint, which concerns survival with a functioning graft by Month 12.

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

The posted results describe outcomes among participants assigned to three immunosuppression groups in a randomized, parallel-group trial. For the primary endpoint, the observed Month 12 percentages are 92.8% for cyclosporine, 96.5% for belatacept LI, and 95.4% for belatacept MI. The unadjusted recalculated confidence intervals for the risk differences include zero, leaving uncertainty about the direction and size of the group contrasts under those calculations.

The sponsor-reported analyses are classified as non-inferiority or equivalence analyses, but the non-inferiority margin and decision rule are not reported in the registry record. The classification alone is not enough to determine whether a prespecified non-inferiority criterion was met. The sponsor’s reported confidence intervals and the recalculated intervals also reflect different methods and interval levels, so one should not treat them as interchangeable.

These results do not establish that belatacept is superior, equivalent, or inferior to cyclosporine across all outcomes. Nor do they establish that the groups have identical outcomes. An estimate is a summary of observed data with uncertainty, and the primary endpoint combines survival with a defined set of graft-loss criteria at a particular follow-up time.

The result also does not answer every question about kidney function, longer-term graft status, adverse events, or patient experience. Secondary measures address some of these issues, but they differ in definitions and follow-up and are subject to the limitations of multiple comparisons and incomplete reporting. No treatment recommendation follows from these registry results alone. Their interpretation is bounded by the outcomes, populations, methods, and follow-up documented in the registry record.

18. Why This Trial Matters Statistically

BENEFIT illustrates why statistical interpretation should distinguish a group percentage from a between-group comparison. The arm-specific values describe the observed outcome in each group, while the risk difference directly represents the estimated contrast. Confidence intervals then show how much uncertainty surrounds those estimates. Reading all three together avoids treating a point estimate as an exact or definitive treatment effect.

The trial also highlights the importance of matching the statistical question to the analysis. A non-inferiority or equivalence analysis is not interpreted in the same way as a test for any difference. Its conclusion depends on a prespecified margin and decision rule. Although the registry labels the sponsor analyses as non-inferiority or equivalence, the margin is not reported, so the key criterion cannot be checked from the registry record.

Another important lesson is that the primary endpoint is a composite of survival and functioning graft status. This creates a clinically interpretable summary, but it can conceal which component drives the result. Separate measures of kidney function and safety can add context, yet multiple secondary analyses require cautious interpretation and clear attention to their timeframes and uncertainty.

Finally, the distinction between a trial’s own analysis and an unadjusted recalculation matters. Recalculation helps readers understand the posted summaries, but it cannot recreate missing design or analysis details. Transparent reporting of analysis populations, missing-data handling, multiplicity plans, and non-inferiority criteria is essential for judging how strongly trial estimates answer their intended questions.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific details needed for a complete appraisal are not reported in the registry record. These include the original sample-size justification, the non-inferiority margin, detailed primary analysis methods, the detailed randomization procedure, and who was masked. The registry’s intervention descriptions provide the treatment names and LI or MI labels but not further regimen details.

The primary endpoint is a composite outcome. Although its definition is detailed, a breakdown of the primary result by physical graft loss, functional graft loss, and participant survival is not reported in the registry record. The endpoint therefore cannot show which component accounts for the group percentages. It also does not describe kidney function among participants who met the functioning-graft definition.

Follow-up windows and denominators vary among the primary and secondary outcomes. Reasons for outcome-specific denominator differences, the handling of incomplete follow-up, and sensitivity analyses for missing data are not reported in the registry record. The safety information includes counts and selected serious-event terms, but the full event definitions, timing, and detailed exposure or follow-up context are not reported in the registry record.

The registry lists many outcomes and analyses but does not report a multiplicity plan or a complete statistical analysis plan. As a result, secondary findings should not be treated as though every comparison had the same confirmatory status. The available registry information supports description of the posted estimates and cautious statistical interpretation, but does not resolve these reporting gaps.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Belatacept Evaluation of Nephroprotection and Efficacy as First-line Immunosuppression (BENEFIT) — NCT00256750.
• Registry record last updated 2016-08-19; status last verified 2016-07.
• Results first posted 2016-08-19.
• 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

BENEFIT is a completed randomized, single-masked, parallel-group Phase 3 trial sponsored by Bristol-Myers Squibb. It enrolled 738 and compared cyclosporine with belatacept LI and belatacept MI after kidney transplantation.

The primary outcome was survival with a functioning graft by Month 12. The posted percentages were 92.8% for cyclosporine, 96.5% for belatacept LI, and 95.4% for belatacept MI. Recalculated unadjusted risk-difference intervals include zero for both comparisons. The registry classifies the sponsor’s primary analyses as non-inferiority or equivalence, but the margin and detailed analysis method are not reported in the registry record. Secondary outcomes cover kidney function, graft-related findings, antibodies, and safety; multiplicity and missing-data procedures are not reported in the registry record.