Efficacy and Safety of Everolimus+EC-MPS After Early CNI Elimination vs EC-MPS +Tacrolimus in Renal Transplant Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Everolimus+EC-MPS After Early CNI Elimination vs EC-MPS +Tacrolimus in Renal Transplant Recipients (NCT00965094), a randomized phase 4 study. The primary outcome is Renal Function Assessed as Glomerula Filtration Rate (GFR) - Nankivell Method - 9 Months After Renal Transplantation (LOCF).

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase 4 trial with no masking. The registry lists total enrollment as 36 and marks the study as completed. It names chronic renal failure as the condition and describes the intended population as de novo renal transplant patients. The trial compared an everolimus regimen after early calcineurin inhibitor elimination with a reference regimen based on tacrolimus. The official title also identifies EC-MPS as part of both regimens.

The primary objective concerned renal function 9 months after transplantation. The primary outcome was glomerular filtration rate measured using the Nankivell method. The registry’s primary outcome population is defined as randomized patients who received at least one dose of study medication after randomization and had at least one post-baseline assessment of the primary efficacy variable. The reported primary outcome groups each contain 15 participants. The registry record does not explain how these analysis counts relate to total enrollment.

The result is therefore best read as an outcome comparison between the two randomized arms among the stated primary analysis population, not as a complete account of every randomized participant’s follow-up. The registry record does not report the randomization procedure, allocation concealment, the intended recruitment target by arm, or the original sample-size justification. The trial is identified as unmasked, so participants and study personnel were not described as blinded to treatment assignment. The registry record does not report whether outcome assessors were separately masked.

The dates recorded are a study start in 2009-12 and primary completion in 2013-06. These dates do not by themselves describe the duration of follow-up for each participant. The primary endpoint timeframe is stated as 9 months. Further protocol details about treatment duration, adherence, or changes in immunosuppressive therapy are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population comprised all randomized patients who received at least one dose of the study medications after randomization and had at least one post-baseline assessment of the primary efficacy variable (renal function based on Nankivell method).

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: Enrolled patient population included all patients who signed an informed consent regardless whether renal transplanation as performed or not.

6. Primary Endpoint

The registry lists the primary outcome as Renal Function Assessed as Glomerula Filtration Rate (GFR) - Nankivell Method - 9 Months After Renal Transplantation (LOCF), measured over 9 months.

The primary endpoint was renal function at 9 months after renal transplantation, expressed as glomerular filtration rate in mL/min/1.73m^2 and calculated using the Nankivell method. The reported summary is a group mean with standard deviation. The registry describes glomerular filtration rate as a clinical estimate of renal function and explains that the Nankivell equation was selected for use in renal transplant patients. The endpoint therefore represents a continuous measure of kidney function rather than an event count.

The registry states that the Nankivell method had been validated in renal transplant patients against a radionuclide measurement of true glomerular filtration rate. This provides the stated rationale for using the equation in this population. The primary analysis used last observation carried forward, meaning that the last available measurement was carried forward for participants without a measurement at the target assessment, according to the registry description. The registry record does not report how many participants required this imputation or how missing observations were distributed between arms.

The study’s stated objective was to assess non-inferiority of the calcineurin-inhibitor-free regimen relative to the tacrolimus-based regimen. A continuous renal-function endpoint can support such a comparison, but interpretation depends on the prespecified non-inferiority margin and analysis plan. Those details are not reported in the registry record. The endpoint values and their uncertainty can be described, but the formal non-inferiority conclusion cannot be reconstructed from the stated objective alone.

7. Results Posted in the Registry

• Everolimus: mean 15.00 versus 16.60 on control; difference -1.60 (95% CI -7.90 to 4.70), standardized effect d = -0.18; z-test p = 0.619.

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.

Assessment of GFR by the Cockcroft-Gault Method (LOCF)

• 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:
  • Everolimus: mean 72.60 versus 72.70 on control; difference -0.10 (95% CI -14.21 to 14.01), standardized effect d = -0.01; z-test p = 0.989.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Everolimus and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes listed in the registry cover several different aspects of renal function and transplant outcomes. They include glomerular filtration rate assessed by the Cockcroft-Gault method, biopsy-proven acute rejection, graft loss or death, treatment failure, and change in renal function described as creatinine slope. A posted numerical comparison is available for the Cockcroft-Gault measure at 9 months; the registry record does not report numerical results for the other listed secondary outcomes.

The available Cockcroft-Gault result follows the same broad pattern as the primary endpoint in that the reported group means are close and the recalculated comparison is not statistically distinguishable from zero. It is a different renal-function measure, expressed in mL/min rather than mL/min/1.73m^2, and should not be treated as a replication of the Nankivell endpoint. Differences in the calculation method and units matter when relating the outcomes. The result does not resolve the primary non-inferiority question, especially because the formal margin and analysis are not reported.

Secondary outcomes can add context, but multiple outcomes create multiple opportunities to observe apparently notable results by chance. In general, when many hypotheses are assessed, unadjusted p-values do not control the overall chance of false-positive findings across the set. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting secondary endpoints. The secondary results should therefore be treated as exploratory or supportive rather than as independent confirmation of a treatment effect.

The absence of posted numerical results for several listed outcomes also limits any assessment of the broader clinical pattern. Their inclusion as planned or listed outcomes does not establish that differences were absent; it means the corresponding results are not reported in the registry record. Taken together, the available secondary information supplies limited additional evidence beyond the primary renal-function comparison.

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

• Assessment of GFR by the Cockcroft-Gault Method (LOCF)
• Participants Who Had Occurrence of Biopsy Proven Acute Rejection, Graft Loss or Death.
• Participants Who Had Occurrence of Treatment Failure.
• Change in Renal Function (Creatinine Slope)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant’s renal function is represented by a numerical glomerular filtration rate, and the registry summarizes each arm using a mean and standard deviation. A mean describes the arithmetic center of the observed values. A standard deviation describes how dispersed those values are around the mean. The standard deviation is not the uncertainty of the estimated mean; uncertainty about the mean comparison is instead conveyed by the confidence interval for the difference.

Mean difference and direction

The recalculated comparison is expressed as the mean in the everolimus arm minus the mean in the reference arm. The estimate of -1.6 mL/min/1.73m^2 therefore indicates that the observed mean was lower in the everolimus arm by that amount. This is a difference between group averages, not a statement about every participant, and it does not by itself identify a clinically important difference. Clinical importance would require an agreed threshold or context, which is not reported in the registry record.

The reported confidence interval runs from -7.902 to 4.702 mL/min/1.73m^2. In general, a confidence interval describes the uncertainty associated with an estimate under the statistical procedure used: it identifies values reasonably compatible with the observed data and the procedure’s assumptions. It is not a range guaranteed to contain the true value, and it is not a probability statement about the treatment effect after the data have been observed. The interval’s inclusion of zero means the recalculated results do not clearly distinguish the group means at the conventional two-sided threshold. The interval also includes differences that could matter in either direction, so absence of a clear difference is not evidence of equivalence.

What the p-value says

The recalculated p-value is 0.619. In general, a p-value describes how unusual data at least as discordant with a specified null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. Here the p-value belongs to an unadjusted recalculation of a mean comparison, not to a reported sponsor analysis of the trial’s stated non-inferiority objective.

Non-inferiority questions require a different interpretive reference point from a simple test for any difference. The analysis must compare the estimated effect and its uncertainty with a prespecified margin that defines the largest acceptable disadvantage. If that margin is not known, the confidence interval cannot be classified against the trial’s formal non-inferiority boundary. The margin, a formal test, and the detailed statistical plan are not reported in the registry record.

Unadjusted recalculation

The comparison statistics are recalculated from the posted arm-level summaries. They are not identified as the sponsor’s own analysis. The registry record reports no analysis entries. The recalculation gives a simple, unadjusted comparison and does not incorporate any covariates, stratification factors, repeated-measure structure, or other adjustments. Whether the original study analysis used any of those methods is not reported in the registry record. The discrepancy indicator is false, so no conflict between a recalculation and a sponsor result is flagged; nevertheless, the recalculation should not be mistaken for a formal protocol analysis.

General statistical reasoning also cautions that a small group size can make estimates sensitive to individual observations and can leave substantial uncertainty. That concern is relevant when interpreting the 15 participants reported in each primary outcome group, but the registry record does not give participant-level data with which to assess skewness, outliers, or the distributional assumptions of a mean-based analysis.

Last observation carried forward

The primary outcome used last observation carried forward, abbreviated LOCF in the registry description. In general, this approach substitutes a participant’s most recent available outcome for a later missing outcome. It can preserve participants in an analysis when the target-time measurement is unavailable, but it relies on a strong assumption that the carried-forward value is a reasonable stand-in for the unobserved value. If renal function changes after the last measurement, carrying the earlier value forward may not represent the participant’s status at 9 months. The registry record does not report how many values were carried forward or provide sensitivity analyses using alternative approaches.

The primary population was not defined simply as every randomized participant. It included randomized patients who received at least one post-randomization dose and had at least one post-baseline primary efficacy assessment. This definition is important for interpreting the estimate and for comparing the analysis with other populations, such as all randomized participants. The registry record does not report results for an alternative analysis population.

11. Confidence Intervals and Precision

The recalculated mean difference in the primary endpoint was -1.6 mL/min/1.73m^2, with a 95% confidence interval from -7.902 to 4.702. The interval covers both negative and positive values, including zero. It therefore does not establish a clear direction for the underlying mean difference. Its breadth also means that the data are compatible with a range of effects rather than tightly identifying a single value.

In general, precision concerns how narrowly an estimate is determined by the data and statistical method. A narrow confidence interval indicates less uncertainty under the method’s assumptions; a wide interval indicates more. Here, the primary outcome analysis includes 15 participants per arm, and the observed standard deviations are 10.3 and 7.0 mL/min/1.73m^2. The interval should be considered alongside those group sizes and the variability in the outcome, rather than interpreted through the p-value alone.

The interval is a recalculated, unadjusted interval based on the posted summary statistics. It is not identified as a confidence interval from a sponsor-reported analysis. The registry record does not report a non-inferiority margin, so the interval cannot be judged against the trial’s intended non-inferiority boundary. A confidence interval that includes zero does not itself rule out non-inferiority, just as it does not demonstrate non-inferiority; the relevant comparison would be with the prespecified margin under the planned analysis.

Precision is also specific to the recorded endpoint, analysis population, and 9-month timeframe. It does not describe uncertainty about longer-term renal function, adverse outcomes, or the full target population beyond the participants represented in the analysis.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrative calculations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the displayed planning quantities are participants per arm, not total events. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario sets the effect to detect at the stated fraction of the observed effect. The trial’s own sample-size justification and original planning assumptions are not reported in the registry record.

The 80% power column represents the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the chosen effect under those assumptions, if that effect were the true effect. The 90% power column uses a higher target probability of detecting the chosen effect, so it calls for a larger planned sample under the same assumptions. These are design-planning quantities, not descriptions of the number enrolled or analyzed in the trial.

The scenarios vary the effect being targeted: 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so the calculation requires more participants per arm. The primary endpoint’s observed mean difference is small relative to its variability, and the resulting planning illustrations are correspondingly large. This dependence on the observed estimate also means the calculations should not be treated as a definitive recommendation for a future study; a future design would need a clinically justified target effect and prespecified design choices.

These figures are not observed power. They are hypothetical planning estimates under the stated assumptions and do not tell how likely the completed trial was to produce a significant result after its data were collected. They also do not establish whether the original trial was adequately sized for its non-inferiority objective, because that objective requires a prespecified margin and a design justification that are not reported in the registry record.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.600; pooled standard deviation σ = 8.806.
2. n = 2 × (1.96 + 0.842)² × 8.806² / -1.600² = 475.5, rounded up to 476 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
delta <- -1.6                      # observed difference in means
sigma <- 8.80596388818396                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(965094)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 476 (80% power), 637 (90% power)
 75% of observed effect: n per arm = 846 (80% power), 1,132 (90% power)
 50% of observed effect: n per arm = 1,903 (80% power), 2,547 (90% power)
power.t.test: 476.5 
Simulated power at n = 476 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 a primary renal-function endpoint and several secondary outcomes, but it does not report how the statistical plan handled multiple comparisons. When multiple outcomes or analyses are tested, the chance of at least one apparently unusual result can increase. General methods for addressing multiplicity include adjusting significance thresholds or specifying a hierarchy of outcomes, but whether either approach was used in this trial is not reported in the registry record. The numerical secondary results should consequently be interpreted cautiously and should not be treated as confirmatory evidence without a stated plan.

The registry record also does not report an interim-analysis plan, stopping rules, or a detailed statistical analysis plan. These items should not be inferred from the trial’s phase or design labels. The stated objective was non-inferiority, but the margin, formal test, and decision rule are not reported. Those omissions prevent a reader from determining the exact criterion against which the primary result was intended to be judged.

For the primary analysis, the registry specifies a population of randomized participants who received at least one dose after randomization and had at least one post-baseline assessment of the primary efficacy variable. This is the population represented by the posted primary outcome results. The registry record does not report results for all randomized participants regardless of treatment received or outcome availability, nor does it describe a per-protocol analysis. For a non-inferiority question, the analysis population and handling of protocol deviations can be especially relevant; the record does not provide enough detail to assess those issues.

Missing primary outcome values were handled using last observation carried forward. In general, this method assumes the last observed value remains an adequate substitute for the missing target-time value. That assumption may not hold if outcomes change between observations. The number of participants with missing target-time measurements, the timing of their last observations, and sensitivity analyses under alternative assumptions are not reported in the registry record. The listed method therefore clarifies the stated imputation approach but not how strongly the result depends on it.

The registry record gives no original sample-size justification or stated assumptions for the non-inferiority design. The illustrative planning calculations based on the observed effect do not fill that gap. Without the planned margin, target effect, and analysis assumptions, the adequacy of the original design for its stated objective cannot be evaluated from the posted record.

15. 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: blood creatinine increased (17.6%), transplant rejection (10.5%), diarrhoea (5.9%), vomiting (5.9%), pyrexia (5.9%).

The safety figures use different at-risk counts from the primary efficacy results. For serious adverse events, the registry lists 19 participants at risk in the everolimus group and 17 in the reference group, with 7 affected in each group. These are counts of participants recorded as affected, not event rates calculated for a common denominator. The record does not explain why these safety denominators differ from the primary outcome analysis counts, so the groups should be read using their own listed at-risk totals.

The registry also lists other adverse events affecting 19 of 19 at-risk participants in the everolimus group and 15 of 17 in the reference group. These figures should not be combined with the serious-event counts: they refer to a separate adverse-event category in the record. The most frequently listed serious adverse-event terms include increased blood creatinine at 17.6% and transplant rejection at 10.5%; diarrhoea, vomiting, pyrexia, and urinary tract infection are each listed at 5.9%. The registry record does not give arm-specific percentages for these terms in the available summary.

Deaths are not reported in the registry record. These summaries describe recorded events in this trial and do not establish causation. Differences in counts should be interpreted in light of the small groups and the absence of fuller information about event ascertainment, exposure time, and severity.

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

The posted primary results describe average renal function at 9 months among the participants included in the specified analysis. The recalculated mean difference is -1.6 mL/min/1.73m^2 for everolimus relative to reference therapy, and its 95% confidence interval ranges from -7.902 to 4.702. The interval includes zero and remains wide enough to leave substantial uncertainty about the size and direction of the underlying difference. The results do not provide a precise estimate of how the regimens compare beyond that observed summary.

These results do not establish that the two regimens are equivalent. They also do not, by themselves, establish or rule out non-inferiority. The stated study objective was non-inferiority, but the registry record does not report the margin or formal analysis needed to apply that criterion. A non-significant unadjusted test for a difference answers a different statistical question from a non-inferiority test.

The outcome concerns a calculated measure of renal function at a specified follow-up time. It does not represent every aspect of kidney health, all transplant outcomes, longer-term function, or the balance of benefits and harms. The registry record lists rejection, graft loss or death, treatment failure, and creatinine slope among secondary outcomes, but numerical results for most of these outcomes are not reported in the registry record. Safety counts are also limited summaries and should not be interpreted as proof that an event was caused by a treatment.

General interpretation should also account for the analysis population and missing-data method. The primary results include participants who met the registry’s post-randomization dose and assessment criteria, and LOCF was used for the endpoint. The record does not provide the number of imputed values or alternative analyses that would show how sensitive the findings are to those choices.

Accordingly, the most supportable conclusion is descriptive: the observed group means were close, and the unadjusted recalculation is imprecise. The posted results do not settle the intended non-inferiority question or support conclusions beyond the measured endpoint, population, and follow-up timeframe.

17. Why This Trial Matters Statistically

This trial illustrates why the wording of a statistical objective matters. The primary aim was non-inferiority, not simply detection of any difference between treatment groups. A conventional difference test and a non-inferiority assessment use different decision criteria. Without the prespecified margin and formal analysis, a non-significant p-value cannot be read as evidence that the experimental regimen met the trial’s stated objective.

The posted data also show the importance of reporting uncertainty alongside point estimates. The mean difference is a single summary, while the confidence interval conveys that the observed data remain compatible with a range of possible effects. In a small analysis population, the interval can be broad even when the group means appear close. Statistical interpretation should therefore consider the estimate, its precision, the endpoint’s clinical context, and the design objective together.

The record provides another useful distinction between trial results and planning calculations. Illustrative sample-size figures based on the observed effect are not a record of the original design assumptions and are not observed power. They demonstrate, in general, how the target effect and desired power influence planning, but they cannot answer whether the completed trial was designed adequately for non-inferiority.

Finally, the registry highlights how analysis populations, imputation, secondary outcomes, and multiplicity shape interpretation. The primary result uses a specified subset of randomized participants and LOCF; the record does not report sensitivity analyses or a multiplicity strategy. These are not minor technical details: they determine how broadly and confidently the estimates can be interpreted. The statistical lesson is to distinguish what the data estimate from what the trial was designed to establish.

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.

Several limitations are specific to the information recorded for this trial. The total enrollment is 36, while the primary endpoint results list 15 participants in each arm. The registry record does not explain the relationship between total enrollment and the primary analysis counts, so the reasons for the difference cannot be determined from the record. Safety results use their own at-risk counts, which should not be assumed to match the efficacy population.

The main statistical limitation is that the registry does not report the non-inferiority margin, formal test, or original design justification. Since non-inferiority was the stated primary objective, these missing details prevent a direct assessment of whether the intended criterion was met. There is no reported sponsor analysis entry with which to compare the simple unadjusted recalculation from the posted summary statistics.

The primary endpoint uses LOCF, but the registry does not state how many observations were carried forward or give sensitivity analyses. It also does not report participant-level data, so the distribution of outcomes, influence of individual observations, and assumptions underlying the mean comparison cannot be examined. The reported primary analysis population excludes randomized participants who did not meet the stated dose and post-baseline assessment criteria; the record does not provide an alternative population analysis.

The study was unmasked, and the record does not say whether outcome assessors were separately blinded. Several secondary outcomes are listed without numerical results, while the record does not state a multiplicity strategy. Treatment descriptions are truncated, limiting reconstruction of the detailed regimens. Finally, the primary outcome timeframe is 9 months; the posted results do not establish longer-term renal function or outcomes beyond the measures reported.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Everolimus+EC-MPS After Early CNI Elimination vs EC-MPS +Tacrolimus in Renal Transplant Recipients — NCT00965094.
• Registry record last updated 2014-08-15; status last verified 2014-08.
• Results first posted 2014-08-15.
• 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

The registry identifies a completed randomized, parallel-group phase 4 trial with no masking and total enrollment of 36. It compared an everolimus-based regimen after early calcineurin inhibitor elimination with a tacrolimus-based reference regimen in de novo renal transplant recipients. The primary objective concerned non-inferiority in renal function at 9 months after transplantation.

The primary endpoint was mean glomerular filtration rate calculated using the Nankivell method. The reported group means were 15.0 mL/min/1.73m^2 for everolimus and 16.6 mL/min/1.73m^2 for reference therapy. An unadjusted recalculation estimated a mean difference of -1.6, with a 95% confidence interval from -7.902 to 4.702 and p = 0.619. The primary analysis used LOCF and included 15 participants per arm.

The registry record does not report the non-inferiority margin, original sample-size justification, detailed statistical plan, or numerical results for most listed secondary outcomes. The posted comparison is therefore informative about the observed endpoint and its uncertainty, but it does not establish the formal non-inferiority conclusion.