Tacrolimus/Everolimus Versus Tacrolimus/Enteric-Coated Mycophenolate Sodium: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tacrolimus/Everolimus Versus Tacrolimus/Enteric-Coated Mycophenolate Sodium (NCT01680861), a randomized phase 3 study. The primary outcome is BPAR (Biopsy-proven Acute Rejection) Incidence During the First 12 Months Post-transplant.

2. Clinical Question

The clinical question is framed around an event count: the number of participants with a biopsy-proven acute rejection during the specified follow-up period. The registry also identifies chronic allograft injury, graft loss, renal function, and discontinuation of study medication as secondary outcomes. Those outcomes provide additional context about the trial's objectives, but they do not change the definition of the primary endpoint.

The registry describes the study as a phase 3 randomized trial in adult primary kidney transplantation. The rationale in its brief summary concerns strategies intended to reduce calcineurin-inhibitor exposure while using another immunosuppressive medicine. That rationale describes the investigators' aims; it is not itself evidence of an outcome. The posted results address observed outcomes in the enrolled trial and should be read separately from the proposed biological or clinical rationale.

3. Trial Design

The registry describes a randomized, open-label, parallel-group phase 3 trial. The two arms were tacrolimus/everolimus and tacrolimus/EC-MPS. Randomization means assignment was intended to use a chance-based process, while open-label means masking was not used. The registry record does not report further details of the randomization procedure, allocation concealment, or any stratification factors.

The record lists an enrollment of 32. The primary endpoint results list 15 participants in each arm, and the secondary results also list 15 in each arm where results are posted. These entries are reported as recorded; the reason the enrollment figure differs from the outcome arm counts is not reported in the registry record. Analysis populations, participant flow, and the handling of participants who did not complete follow-up are also not reported in the registry record.

The trial status is completed. The recorded start is 2012-11, and primary completion is recorded as 2014-12. The official title identifies the setting as adult primary kidney transplantation and describes the intended comparison as prevention of biopsy-proven acute rejection and chronic allograft injury. These title and registry entries identify the scope of the study but do not establish how the treatments performed.

Both arm descriptions refer to reduced tacrolimus dosing. The intervention list also includes corticosteroids, but complete dosing, treatment duration, adherence procedures, and permitted concomitant treatments are not reported in the registry record. The registry lists the sponsor as Gaetano Ciancio. Details of the original sample-size justification, planned interim analyses, protocol deviations, and prespecified statistical analysis plan 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.

Early Post-transplant Period

Reasons for not completing this period:

First 12 Months Post-transplant

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 BPAR (Biopsy-proven Acute Rejection) Incidence During the First 12 Months Post-transplant, measured over 1 year.

The primary endpoint is the incidence of biopsy-proven acute rejection during the first 12 months after transplantation, reported as the number of participants with the event. A biopsy provides tissue for assessment, and the registry states that rejection grading used standard Banff criteria. The endpoint therefore concerns rejection that was biopsy-proven under the stated grading approach, rather than every possible clinical suspicion of rejection.

Counting participants with an event gives a direct summary of how often the endpoint occurred in each randomized arm during the stated period. It is a binary outcome at the participant level: a participant either met the endpoint definition or did not. This kind of outcome can be compared as a difference in event risk, while a time-to-event approach can also use information about when events occur, if that timing is available and the analysis is defined accordingly.

In general, a biopsy-based endpoint can make the outcome definition more specific than a diagnosis based only on symptoms or clinical judgment. It also depends on biopsy practice and the criteria used to classify findings. The registry states the Banff grading basis, but does not report biopsy schedules, criteria for obtaining biopsies, or whether outcome adjudication was independent of treatment assignment. Those procedural details are not reported in the registry record.

The endpoint was chosen to address acute rejection within the first post-transplant year, one of the objectives named in the trial title. The result is limited to this endpoint and follow-up period; it does not by itself summarize longer-term graft function, chronic injury, graft loss, safety, or the overall balance of outcomes.

7. Results Posted in the Registry

• Tacrolimus/EC-MPS: 20.0% (3/15) versus 6.7% (1/15) on control; risk difference 13.3 percentage points (95% CI -10.5 to 37.2), risk ratio 3.00 (0.35–25.68); unadjusted two-proportion z-test p = 0.283.

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.

Incidence of Chronic Allograft Nephropathy (CAI) at 12 Months Post-transplant

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tacrolimus/EC-MPS: 20.0% (3/15) versus 20.0% (3/15) on control; risk difference 0.0 percentage points (95% CI -28.6 to 28.6), risk ratio 1.00 (0.24–4.18); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tacrolimus/EC-MPS and the control. The interval gives the range of effects that remain compatible with the data.

eGFR (Calculated Glomerular Filtration Rate), i.e., Renal Function, at 1 Month Post-transplant.

• 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 errors.
• Result:
  • Tacrolimus/EC-MPS: mean 62.10 versus 82.10 on control; difference -20.00 (95% CI -40.15 to 0.15), standardized effect d = -0.71; z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tacrolimus/EC-MPS and the control. The interval gives the range of effects that remain compatible with the data.

eGFR (Renal Function) at Month 3 Post-transplant

• 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 errors.
• Result:
  • Tacrolimus/EC-MPS: mean 65.60 versus 75.70 on control; difference -10.10 (95% CI -24.45 to 4.25), standardized effect d = -0.50; z-test p = 0.168.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tacrolimus/EC-MPS and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the study's focus beyond acute rejection to chronic allograft injury, graft loss, renal function at multiple follow-up times, and discontinuation of study medication. The registry lists six secondary outcomes. Numeric results are posted for chronic allograft injury at 12 months and eGFR at 1 and 3 months. Results for graft loss, eGFR at 6 months, and discontinuation are not reported in the registry record.

Across the posted secondary results, the pattern is not a uniform contrast across outcome types or follow-up times. The chronic allograft injury event counts are the same in the two arms, while the renal-function summaries show different arm means at the reported visits. These outcomes measure distinct constructs: an event count, a measure of kidney function, and other clinical or treatment outcomes. They should not be combined into a single claim about the comparative effect.

These secondary outcomes provide context for the primary BPAR result but cannot resolve its uncertainty. A result on renal function does not establish the effect on biopsy-proven rejection, and a similar count for chronic injury does not establish equality of the underlying risks. The endpoints differ in definition, measurement scale, and follow-up. No overall composite or synthesis across these outcomes is reported in the registry record.

Unadjusted secondary results carry less weight for confirmatory interpretation when multiple outcomes are examined. Each additional comparison can increase the chance of at least one apparently notable finding even if there is no corresponding effect. The registry does not report a multiplicity adjustment, a prespecified hierarchy for secondary endpoints, or a complete account of the planned analyses. The secondary pattern is therefore best treated as descriptive and hypothesis-generating rather than as independent confirmation of the primary result.

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

• Incidence of Chronic Allograft Nephropathy (CAI) at 12 Months Post-transplant
• Graft Loss (Return to Permanent Dialysis or Death)
• eGFR (Calculated Glomerular Filtration Rate), i.e., Renal Function, at 1 Month Post-transplant.
• eGFR (Renal Function) at Month 3 Post-transplant
• eGFR (Renal Function) at 6 Months Post-transplant
• Discontinuance of Any Study Medication (Tacrolimus, Everolimus, or EC-MPS)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference mean?

A risk difference compares the proportion of participants with an event in one arm with the proportion in the other. A positive value for the comparison as defined in the recalculation means the event proportion was higher in the EC-MPS arm; a negative value would indicate the reverse. A value of zero represents equal observed proportions. In this trial's primary recalculation, the estimate is 0.133, with the comparison ordered as EC-MPS relative to everolimus.

The risk difference is an absolute measure: it describes the size of the difference between event risks on the same scale. It differs from a risk ratio, which compares risks multiplicatively, and an odds ratio, which compares event odds. Relative measures can look large when events are uncommon, while the absolute measure keeps attention on the difference in event frequency. None of these measures alone resolves the uncertainty in a small dataset.

What does a confidence interval communicate?

A confidence interval gives a range of values compatible with the data under the statistical procedure used. It is an indication of precision, not a guarantee that the true effect lies within a particular realized interval. A narrow interval indicates greater precision than a wide interval, all else equal. The primary risk-difference interval runs from -0.105 to 0.372 and includes zero; its breadth reflects substantial uncertainty about the size and direction of the underlying difference. The confidence level for the posted intervals is not reported in the registry record.

How should the p-values be read?

A p-value is calculated under a statistical model that specifies a null hypothesis and other assumptions. It measures how unusual data at least as discrepant as those observed would be if that model were correct. It does not measure the size or clinical importance of an effect, and it is not the chance that the null hypothesis is true. Interpretation depends on the analysis method, outcome definition, and analysis plan. The registry reports p = 0.32 for the primary log-rank analysis and the unadjusted recalculation gives p = 0.283; these values arise from different approaches and are not interchangeable.

Why can time-to-event and count comparisons differ?

A count-based comparison uses whether participants experienced an event within the outcome window. A time-to-event method can use the timing of events and, depending on the analysis, account for differing follow-up or censoring. The log-rank test is a method for comparing event-time patterns. The registry does not report the event times, censoring details, or analysis population needed to examine how those features affected the reported analysis. It would therefore be speculative to attribute the difference between the reported and recalculated p-values to a particular data feature.

What does the unadjusted recalculation represent?

The recalculated measures use posted arm-level summary statistics and do not adjust for other variables. Such calculations help express the observed contrast in familiar statistical terms, but they cannot reproduce an analysis that uses participant-level data, covariate adjustment, event times, or additional protocol details. The recalculated result is not a substitute for the sponsor's reported analysis. The registry does not report enough information to verify any model assumptions or reproduce the sponsor analysis in full.

Why does sparse information matter?

When event counts are small, the estimate can change materially with a small change in observed events. Uncertainty intervals can consequently be broad, and a single summary value may give an overly definite impression. General statistical practice calls for considering the estimate, interval, event counts, and design together rather than treating a p-value as a complete account of evidence. Methods for sparse binary data can also have different properties from large-sample approximations; the registry does not report a detailed rationale for the method used in its primary analysis.

What does over-dispersion mean in general?

Over-dispersion arises when observed variability exceeds what a statistical model assumes. It is especially relevant to some count and clustered-data models, because underestimated variability can make uncertainty appear too small. The primary endpoint is reported as participants with an event, not as a repeated count process, and the registry does not report an over-dispersion model. This general concept should not be taken to imply that over-dispersion was present in this trial.

How do secondary analyses fit?

Secondary outcomes can explore other aspects of the study, but they do not replace the primary endpoint. Each additional comparison creates another opportunity to observe an apparently notable result by chance. If many outcomes are tested, unadjusted p-values do not account for that multiplicity. The registry does not report a multiplicity adjustment or a hierarchy governing confirmatory interpretation. Secondary findings therefore require cautious, exploratory interpretation, especially when the analysis plan and complete outcome reporting are unavailable.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.133 for tacrolimus/EC-MPS relative to tacrolimus/everolimus. Its confidence interval extends from -0.105 to 0.372. The interval covers zero and includes values in both directions, so the data do not precisely locate the underlying difference. The estimated direction is not enough to rule out a smaller contrast or a contrast favoring the other arm.

Precision is limited in part by the small outcome groups and few recorded primary events. With sparse events, even a visible difference in counts can correspond to considerable uncertainty about the underlying event risks. The estimate should be considered together with its interval rather than read as a precise effect size. The interval is not a range of possible observed counts; it describes uncertainty about an effect measure under the recalculation's statistical procedure.

The registry does not identify the confidence level associated with the posted intervals. It also does not report details such as the analysis population, missing observations, or the assumptions used to obtain the sponsor's primary analysis. Those omissions limit how fully the interval can be interpreted or reproduced. The recalcualted interval is an unadjusted result from arm-level summaries and should not be mistaken for an adjusted or time-to-event interval.

In general, a confidence interval is more informative than a point estimate alone because it shows the range of effects reasonably compatible with the data under the method. It does not establish equivalence when it includes zero, and it does not demonstrate that important differences have been excluded. Establishing equivalence or noninferiority would require an appropriate prespecified margin and analysis; those are not reported in the registry record.

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 are expressed as participants per arm for the binary primary endpoint; they are not total event counts. They use the observed effect as a starting point and show planning for 100% of that observed effect, 75% of the observed effect, and 50% of the observed effect. For 100% of the observed effect, the illustration gives 101 participants per arm for 80% power and 135 participants per arm for 90% power. For 75% of the observed effect, it gives 161 participants per arm for 80% power and 215 participants per arm for 90% power. For 50% of the observed effect, it gives 317 participants per arm for 80% power and 424 participants per arm for 90% power.

The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. In plain language, the 80% power column describes a planning target that would give the specified design an 80% chance of detecting an effect of the chosen size under the calculation's assumptions. The 90% column uses a higher chance of detection as its target. Smaller effects require more participants to detect under these assumptions, which is why the planning figures rise as the assumed effect becomes a smaller fraction of the observed effect.

These figures are planning illustrations, not observed power. They are based on an effect estimated from this trial's results and do not establish what the original trial was designed to detect. The original sample-size justification and design assumptions are not reported in the registry record. The calculations should not be interpreted as a recommendation or as evidence that the trial had a particular probability of finding an effect.

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 = 0.067; treatment proportion p₁ = 0.200; average p̄ = 0.133.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4807 = 0.9422.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4714 = 0.3967.
4. n = (0.9422 + 0.3967)² / (0.1333)² = 100.8, rounded up to 101 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 <- 0.0666666666666667                          # control proportion
p1 <- 0.2                          # 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(1680861)
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 = 101 (80% power), 135 (90% power)
 75% of observed effect: n per arm = 161 (80% power), 215 (90% power)
 50% of observed effect: n per arm = 317 (80% power), 424 (90% power)
power.prop.test: 100.8 
Simulated power at n = 101 per arm: 0.818 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a log-rank analysis for the primary BPAR outcome, with p = 0.32. The unadjusted recalculation from the posted arm-level event summaries gives p = 0.283 for the risk-difference comparison. The recalculation is not a reproduction of the log-rank analysis: it uses a different summary and does not incorporate the event-time information used by a time-to-event method. The registry does not report the event-time data or details that would explain the precise relationship between these analyses.

For chronic allograft injury, the sponsor's reported log-rank p-value is 0.99, while the recalculated unadjusted comparison is based on the posted event counts. For eGFR, the reported analyses use two-sided t-tests. The registry reports p = 0.06 at 1 month and p = 0.18 at 3 months; the corresponding unadjusted recalculations give p = 0.052 and p = 0.168. The small numerical differences should be read in light of the distinct procedures and the rounded summary statistics.

The registry does not flag a discrepancy between the reported and recalculated results. The sponsor's reported methods and p-values remain the trial's own analyses; recalculations are descriptive checks based on posted summaries. Without participant-level data and the full statistical plan, neither the exact source of any difference nor the details of the sponsor's implementation can be established.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, and it reports analyses for several outcomes. When several endpoints or comparisons are examined, the chance of observing at least one apparently notable result can increase. Statistical procedures can address this issue through prespecified testing hierarchies, adjusted significance thresholds, or other multiplicity-control strategies. Whether any such approach was planned or used is not reported in the registry record.

The registry does not state whether the primary endpoint was analyzed under an intention-to-treat, per-protocol, or other analysis population. It also does not report how participants with missing endpoint information, withdrawal, loss to follow-up, or protocol deviations were handled. These details matter because the analysis population and missing-data approach can affect the interpretation of an outcome comparison. The arm-level results alone do not show whether every randomized participant contributed to each analysis.

The record lists enrollment as 32 and lists 15 participants per arm in the primary outcome results. The reasons for the difference between the enrollment entry and the arm counts in the outcome results, including any participant flow or exclusions, are not reported in the registry record. No inference should be made from these entries about the number or reasons for missing observations.

The registry reports a log-rank method for the primary outcome and identifies time-to-event analysis, but does not provide event times, censoring details, model diagnostics, or an explanation of how follow-up was treated. It does not report the full statistical analysis plan, interim analyses, or sample-size justification. These omissions constrain assessment of prespecification and reproducibility. They do not demonstrate that the analyses were inappropriate; they mean the record does not contain enough information to evaluate those features.

For the secondary outcomes, the registry reports selected results but not the complete numeric result set for all listed outcomes. The missing results and analysis details prevent a full assessment of selective reporting or the role of unreported outcomes in the interpretation. This uncertainty is an additional reason to distinguish the reported findings from confirmatory evidence.

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 1% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: polyoma viral infection (viremia) (13.3%), nodat (13.3%), urinary tract infection requiring hospitalization (6.7%), ear infection requiring hospitalization (6.7%), pneumonia (6.7%).

The registry reports serious adverse events among 4 participants in each arm, with 15 at risk in each arm. It reports 0 participants affected by other adverse events in each arm, also with 15 at risk. These figures are descriptive counts in the registry record; they do not establish that the overall safety profiles were the same or different. The registry does not provide a comparative statistical analysis of the adverse-event results in the information.

The listed serious adverse-event terms include Polyoma Viral Infection (Viremia) and NODAT, each reported as 13.3%. Urinary Tract Infection Requiring Hospitalization, Ear Infection Requiring Hospitalization, Pneumonia, and Sepsis are each reported as 6.7%. These percentages describe the listed terms, not necessarily the full range of safety outcomes or the risk of every possible event. The record does not explain whether participants could appear under more than one term.

Death counts are not reported in the registry record. Details on event severity beyond the serious-event classification, timing, duration, attribution to study treatment, and exposure-adjusted rates are also not reported. Because the trial outcome groups are small, absence of a reported event in a category should not be read as evidence that the event cannot occur. The safety figures should be interpreted as limited descriptive reporting, not as a complete assessment of comparative safety.

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

The posted primary results show 1 participant with biopsy-proven acute rejection in the tacrolimus/everolimus arm and 3 in the tacrolimus/EC-MPS arm during the first 12 months. The unadjusted risk-difference estimate points toward a higher event risk in the EC-MPS arm, but its confidence interval is wide and includes zero. The sponsor's reported log-rank analysis gives p = 0.32. Together, these findings describe the observed trial data; they do not establish a definitive difference between the regimens.

The results do not demonstrate that the treatments are equivalent. A failure to establish a clear difference is not the same as evidence that meaningful differences have been excluded. The registry does not report an equivalence or noninferiority margin, or a design specifically intended to establish either conclusion. The results also do not prove that either regimen prevents rejection or that either is ineffective.

The trial's small outcome groups and sparse primary events limit precision. The uncertainty interval allows a range of underlying differences, and the registry does not provide information needed to evaluate all aspects of the sponsor's analysis or participant follow-up. The open-label design is part of the study context; whether outcome assessment was masked or independently adjudicated is not reported in the registry record.

The conclusion is limited to the recorded population, interventions, endpoint definition, and follow-up period. The primary result does not answer questions about longer-term graft survival, overall kidney function, chronic injury, all safety outcomes, or treatment adherence. Some secondary results are posted, while results for several listed secondary outcomes are not reported in the registry record.

These statistics are not medical advice and should not be used alone to choose treatment. The clinical meaning of any observed contrast depends on the broader evidence, the study's detailed methods, and relevant clinical considerations, many of which are not available in the registry record. The appropriate statistical conclusion is restrained: the trial records a difference in the primary event counts, but the estimate is imprecise and the reported analyses do not settle the comparative effect.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can still produce substantial uncertainty when the number of participants and observed events is limited. Randomization is designed to support a fair comparison between assigned groups, but it does not guarantee precise estimates in a small study. The primary event counts are low, and the interval around the recalculated risk difference is broad. Reading only the point estimate would hide much of that uncertainty.

It also illustrates why the analysis method matters. The registry reports a log-rank analysis, which addresses event-time information, while the recalculation uses arm-level event counts to estimate an unadjusted risk difference. Both can be informative, but they answer the comparison through different statistical summaries. Without participant-level event times and fuller analysis details, their results cannot be treated as identical or reconciled completely.

The secondary outcomes demonstrate another common challenge: several endpoints can describe different aspects of a clinical question, yet a pattern across them is not automatically a single coherent treatment effect. Multiplicity, selective availability of results, follow-up, and measurement differences all matter. The registry does not report enough about its analysis plan to determine how secondary findings were intended to support the primary conclusion.

Finally, the planning illustrations show how sample-size needs depend on the effect a study aims to detect and the chosen power target. They are distinct from the trial's original design justification, which is not reported in the registry record. Keeping planning calculations separate from observed evidence helps avoid treating a small completed study as though its results alone establish what a future study would find.

19. Limitations

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

Several trial-specific limitations affect interpretation. The registry describes an open-label design, but it does not report whether biopsy assessment or endpoint adjudication was independent of treatment assignment. Because the primary endpoint depends on biopsy and grading, details of biopsy practice and assessment procedures would help readers evaluate possible ascertainment influences; those details are not reported in the registry record.

The primary outcome counts are sparse, and each listed arm contains 15 participants. The resulting risk-difference interval is wide. The registry reports an enrollment of 32, while the primary results list 15 participants in each arm; participant flow and the reason for this difference are not reported in the registry record. Analysis populations, exclusions, missing outcomes, and follow-up completeness are also not reported.

The reported primary method is log-rank, but event-time data, censoring details, and model diagnostics are not reported. The unadjusted recalculation uses only arm-level summary information and cannot assess covariate balance or reproduce participant-level analyses. The original statistical plan, sample-size rationale, and interim-analysis procedures are not reported in the registry record.

The trial compares two multidrug strategies, and both arm descriptions mention reduced tacrolimus dosing. The complete regimens, treatment adherence, changes in treatment, and use of corticosteroids are not described sufficiently in the available record to assess their role. The study's follow-up for the primary outcome is limited to the first 12 months, so the primary result does not establish longer-term outcomes.

Some secondary outcome results are not reported in the registry record, and multiplicity handling is not described. Safety reporting is also limited: deaths, event timing, attribution, and detailed exposure information are not reported. These limitations restrict precision, reproducibility, and the breadth of conclusions that can be drawn, without demonstrating that any particular bias or error occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Tacrolimus/Everolimus Versus Tacrolimus/Enteric-Coated Mycophenolate Sodium — NCT01680861.
• Registry record last updated 2016-12-15; status last verified 2016-10.
• Results first posted 2016-12-15.
• 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.

23. Record Summary

NCT01680861 is a completed, randomized, open-label, parallel-group phase 3 trial comparing tacrolimus/everolimus with tacrolimus/EC-MPS in adult primary kidney transplantation. The recorded start is 2012-11 and primary completion is 2014-12. The primary endpoint is biopsy-proven acute rejection during the first 12 months after transplantation.

The primary results list 1 event in the tacrolimus/everolimus arm and 3 in the tacrolimus/EC-MPS arm, with 15 participants listed per arm. The registry reports a log-rank p-value of 0.32. An unadjusted recalculation gives a risk difference of 0.133, with a confidence interval from -0.105 to 0.372 and p = 0.283. The estimate is imprecise and does not establish a definitive comparative effect.

The registry lists six secondary outcomes but does not report results for all of them. The original design assumptions, analysis populations, missing-data procedures, and multiplicity approach are not reported in the registry record.