Randomized Conversion of Calcineurin-Inhibitors in Renal Allograft Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Conversion of Calcineurin-Inhibitors in Renal Allograft Recipients (NCT00866879), a randomized phase 4 study. The primary outcome is Incidence of Acute Cellular Rejection.

2. Clinical Question

The clinical question is about the comparison of two medication regimens, not about sirolimus in isolation: both groups are described as taking mycophenolate mofetil, while the calcineurin-inhibitor strategy differs. The posted primary result records participants with acute cellular rejection by the reported assessment timeframe. A lower observed event proportion in the continuing-tacrolimus group is reflected in the registry’s comparative estimates, which favor that group on this endpoint. The registry record does not establish why any difference occurred or whether it would apply to patients outside the study population.

The trial also identifies renal allograft function and other outcomes as secondary interests. Those measures address related but distinct questions: rejection is an event outcome, while renal function and the other listed outcomes describe different aspects of transplant status and health. They should not be treated as interchangeable evidence for the primary question. Details of eligibility, baseline clinical characteristics, and the criteria used to define acute cellular rejection are not reported in the registry record.

3. Trial Design

The registry record describes a Phase 4, randomized, parallel-group trial with no masking. It lists enrollment as 275 and status as completed. Northwestern University is named as the sponsor. The recorded start is 2007-06, and primary completion is recorded as 2017-12. The study title describes conversion from tacrolimus to sirolimus 6–24 months after transplant in a prednisone-free immunosuppression regimen.

The control group continued mycophenolate mofetil and tacrolimus. The Transition to Sirolimus Group switched to mycophenolate mofetil and sirolimus. The reported outcome groups contain 90.0 participants in the Control group and 185.0 in the Transition to Sirolimus Group. The registry identifies participants as the unit for the primary endpoint, and reports counts of participants with acute cellular rejection. Donor information and donor blood draws are also listed among study activities, but donors are not one of the two treatment groups used in the primary comparison.

Acute cellular rejection was assessed at 6 months, 12 months, and 24 months; the registry labels the reported timeframe as months 24 reported. Thus, the posted primary result should be read as a result at the specified reported endpoint timeframe, rather than as a full account of the pattern at every scheduled assessment. Details about random-sequence generation, allocation concealment, adherence, treatment discontinuation, crossover, and follow-up completeness are not reported in the registry record.

The registry lists five outcome measures and describes several secondary questions, including renal allograft function, metabolic and safety outcomes, patient and graft survival, and regulatory T cells. Numerical results for some secondary measures are present, but a complete analysis plan and the full set of reported analyses are not recorded. The original sample-size justification, intended statistical model, prespecified analysis populations, and planned handling of missing data are not reported in the registry record. Those omissions limit how fully the randomized design can be evaluated from the registry information alone.

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: Donor participants were no part of our outcome analysis because their participation was only on the basis of providing blood for testing the immune system of the recipients. The analysis of the recipients was intention to treat therefore all recipient participants completed the study period

Overall Study

5. Baseline Characteristics

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

Population: Donor participants were no part of our outcome analysis because their participation was only on the basis of providing blood for testing the immune system of the recipients. The analysis of the recipients was intention to treat therefore all recipient participants completed the study period

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Acute Cellular Rejection, measured over Assessed at 6 Months, 12 Months, 24 Months, months 24 reported.

The primary endpoint is the incidence of acute cellular rejection, measured as the count of participants with an event. The registry identifies participants as the unit and reports the endpoint at the months 24 assessment, after listing assessments at 6 months and 12 months as well. A participant count is a straightforward way to describe how many people in each group experienced the event, but interpretation of the comparison also depends on the number assessed in each group. The posted summaries give those arm-level counts and group sizes.

Rejection is used as the primary endpoint because the stated primary research question is whether the two immunosuppressive regimens differ in acute cellular rejection after kidney transplantation. It is a clinically relevant event for the study’s stated purpose, while renal allograft function is described separately as a secondary outcome. The registry also says the study examines whether switching may better preserve long-term kidney function; that broader aim does not change the identity of the listed primary endpoint.

The endpoint result is not a complete description of transplant outcomes. A count of participants with rejection does not by itself summarize renal function, survival, adverse events, or the timing and recurrence of rejection. Definitions used to adjudicate an acute cellular rejection event, the handling of recurrent events, and the number of participants with missing endpoint assessments are not reported in the registry record. The result should therefore be interpreted as the posted participant-event summary at the stated assessment, rather than as a detailed account of every clinical course.

7. Results Posted in the Registry

• Transition to Sirolimus Group: 16.8% (31/185) versus 7.8% (7/90) on control; risk difference 9.0 percentage points (95% CI 1.3 to 16.7), risk ratio 2.15 (0.99–4.70); unadjusted two-proportion z-test p = 0.043.

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.

Renal Allograft Function Calculated With e-GFR and Proteinuria

• 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:
  • Transition to Sirolimus Group: mean 58.40 versus 57.60 on control; difference 0.80 (95% CI -4.76 to 6.36), standardized effect d = 0.03; z-test p = 0.778.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Transition to Sirolimus Group and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Regulatory T Cells

• 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:
  • Transition to Sirolimus Group: mean 98.00 versus 75.00 on control; difference 23.00 (95% CI 20.86 to 25.14), standardized effect d = 2.36; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Transition to Sirolimus Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address a broader set of questions than the primary rejection endpoint. The registry lists renal allograft function, lipid profile and several health outcomes, patient and graft survival, and regulatory T cells. The posted numerical summaries include renal allograft function and regulatory T cells. The record does not report numerical results for the other listed secondary outcomes in the summaries available for interpretation.

The pattern across the reported secondary measures is not uniform. Renal-function results do not show a clear separation in the reported group averages, while the regulatory T-cell result shows a marked group contrast. These findings relate to different biological and clinical domains and cannot be combined into a single overall judgment about the medication strategies. They also do not resolve the primary endpoint comparison: a secondary laboratory measure does not confirm or negate a difference in acute cellular rejection.

Secondary outcomes are often useful for understanding possible effects beyond the primary question, but they generally carry less confirmatory weight when the analysis plan and multiplicity handling are not reported. Testing many outcomes increases the chance that some comparisons will look notable by chance alone. A prespecified hierarchy or adjustment can address that concern, but neither is documented in the registry record. The secondary p-values should therefore be read as unadjusted statistical summaries, not as a collection of independent confirmations.

The registry record does not provide a complete account of secondary endpoint definitions, timing beyond the stated assessment schedule, missing observations, or model choices. No conclusion about outcomes without posted numerical results can be drawn from their inclusion in the outcome list. Taken together, the available secondary information is descriptive and hypothesis-generating; it does not replace a prespecified, fully reported evaluation of the primary endpoint or the broader benefit-risk profile.

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

• Renal Allograft Function Calculated With e-GFR and Proteinuria
• Evaluate if CI Conversion Impacts on Lipid Profile, Incidence of Hypertension, Malignancies, and Opportunistic Infections and Post-transplant DM
• Patient and Graft Survival
• Percentage of Regulatory T Cells

9. Statistical Interpretation

10. Statistical Methods Explained

The registry gives arm-level counts and group sizes for the primary binary outcome, along with a comparative risk-difference estimate and an unadjusted p-value. The displayed inferential summaries are therefore best understood as an unadjusted comparison of the posted outcome summaries. The registry does not report a detailed sponsor analysis or a prespecified statistical plan, so it is not possible to identify from the record whether the posted comparison was the planned primary analysis or whether other adjustments were intended.

What does a risk difference express?

A risk difference compares the event proportions in two groups by expressing how far apart they are on the absolute-risk scale. A positive estimate for the switching group means the observed event proportion is higher in that group than in the comparator. This scale is often useful for clinical interpretation because it describes an absolute separation in event probability, rather than a relative change. It remains an estimate, however, and its uncertainty matters: the confidence interval describes a range of values compatible with the data and the method used to construct it.

The registry also reports relative measures, including a risk ratio and an odds ratio. A risk ratio compares the event proportions multiplicatively, while an odds ratio compares event odds. These measures answer related but not identical questions and can differ in magnitude. Their interpretation depends on the scale used; neither should be substituted for the absolute-risk comparison without explanation. Different interval estimates can also appear to tell slightly different stories around the null value, especially when they arise from different methods. The registry does not give enough detail to identify the exact methods used for every reported interval.

How should the p-value be read?

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null model and the assumptions of the test were true. 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 primary p-value is explicitly unadjusted. Without a reported testing hierarchy or multiplicity procedure, it should not be treated as a final family-wise assessment across all study outcomes and comparisons.

Randomization is intended to make treatment groups comparable on average at the point of allocation, supporting a causal interpretation when allocation is implemented appropriately and follow-up and analysis preserve the randomized comparison. The registry records randomized allocation, but does not report the sequence-generation method, concealment process, or analysis population. It also does not describe whether participants were analyzed according to assigned group or according to treatment received. Those details are important when interpreting a randomized comparison, especially if adherence or switching between regimens differed.

What do the continuous-outcome summaries add?

For renal allograft function and regulatory T cells, the registry reports group means and standard deviations, with a mean-difference estimate and confidence interval. A mean difference is the separation between group averages on the outcome’s measurement scale. A standard deviation describes variability among measurements within a group; it is not the uncertainty in the estimated mean difference. The confidence interval for a mean difference describes uncertainty about the group contrast under the method used. The registry does not report detailed model specifications for these comparisons.

These continuous-outcome summaries are unadjusted comparisons of group summaries, rather than evidence that accounts for possible baseline differences or repeated measurements. The registry lists assessments at 6 months, 12 months, and 24 months, while the posted summaries identify months 24 as reported. The record does not describe how measurements from earlier visits were handled, whether change from baseline was analyzed, or how any correlation among repeated observations was modeled. Those details cannot be inferred from the reported means alone.

Why can over-dispersion matter in count outcomes?

As a general statistical point, count data may vary more than a simple model expects. This is called over-dispersion. When it is present and ignored, standard errors can be too small, which can make confidence intervals too narrow and p-values appear more decisive than warranted. The primary outcome is reported as participants with an event, not as a recurrent-event count or event rate. The registry does not report a model for recurrent rejection events or an over-dispersion assessment, so such modeling should not be assumed.

In general, model choice should match the outcome’s structure and the study question. Binary event outcomes, continuous measurements, and time-to-event outcomes call for different methods and assumptions. The registry record does not identify a time-to-event analysis for the primary endpoint, despite listing patient and graft survival among secondary outcomes. It also does not report any adjustment covariates, subgroup analyses, or sensitivity analyses. The summary statistics can be described directly, but claims about more complex modeling would go beyond the record.

What is not documented?

The registry does not report the original sample-size justification, the intended statistical analysis plan, the handling of missing observations, or the definitions of the analysis populations. It does not report interim analyses or stopping rules. These are not details that can be reconstructed from a p-value or from the posted group summaries. Their absence does not invalidate the reported numbers, but it limits assessment of whether the analyses followed the original protocol and how sensitive the conclusions might be to alternative reasonable choices.

11. Confidence Intervals and Precision

A confidence interval expresses uncertainty around an estimated contrast. It is not a guarantee that the true value lies in the reported interval, and it does not measure the probability that the treatment strategy is beneficial or harmful. A narrow interval indicates greater statistical precision under the method used; a wide interval indicates that a broader range of effects remains compatible with the data. Precision is separate from clinical importance.

For acute cellular rejection, the registry reports a positive risk-difference estimate and an interval whose endpoints are both positive. The relative risk interval, by contrast, extends across the null value of 1. The odds-ratio interval is reported 1. These measures use different scales and may use different estimation methods; they should be interpreted as distinct summaries rather than forced into a single conclusion. The primary p-value is unadjusted, which is also relevant when considering the strength of evidence.

For renal allograft function, the reported mean-difference interval extends from -4.763 to 6.363 and includes no difference. This indicates uncertainty about the direction and size of the group contrast on the reported scale. For regulatory T cells, the interval extends from 20.86 to 25.14, a more tightly bounded positive contrast. Neither interval alone establishes the broader clinical meaning of the outcome or the reliability of all study analyses.

Confidence intervals depend on assumptions and analysis methods. The registry does not report enough detail to evaluate those methods fully, and it does not provide interval estimates for every listed secondary outcome. Consequently, the apparent precision of the reported estimates should not be confused with completeness of evidence. Missing-data information, prespecified models, and adjustment procedures are also relevant to how much confidence to place in an estimate.

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 figures are planning illustrations based on the observed effect, not a description of the trial’s original design justification. For this binary outcome, the figures are participants per arm. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a design intended to have an 80% chance of detecting the chosen effect under the stated assumptions, if that effect is the true one and the model assumptions hold. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants. These planning figures do not say how likely the observed trial result was to be found after the trial was completed. This is not observed power.

Rows based on 100% of the observed effect use the effect estimate as the target for a future planning exercise. Rows based on 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from random variation and therefore need more participants under otherwise unchanged assumptions. These illustrations are particularly sensitive to the observed effect estimate: if that estimate is imprecise or unusually large, the projected group sizes can be unstable or misleading for planning.

Equal allocation is an assumption in these illustrations, not a description of the observed enrollment pattern. The registry reports different group sizes, and the planning exercise does not reproduce all features of the trial. It also does not account for unreported design choices such as anticipated loss to follow-up, covariate adjustment, or multiplicity. The figures should therefore be treated as conditional examples, not as a recommendation or a retrospective measure of the completed trial’s success.

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 = 0.078; treatment proportion p₁ = 0.168; average p̄ = 0.123.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4639 = 0.9093.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4596 = 0.3868.
4. n = (0.9093 + 0.3868)² / (0.0898)² = 208.4, rounded up to 209 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 <- 0.0777777777777778                          # control proportion
p1 <- 0.167567567567568                          # 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(866879)
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 = 209 (80% power), 279 (90% power)
 75% of observed effect: n per arm = 342 (80% power), 457 (90% power)
 50% of observed effect: n per arm = 702 (80% power), 939 (90% power)
power.prop.test: 208.4 
Simulated power at n = 209 per arm: 0.809 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial used a formal multiplicity strategy. This matters because the record lists several outcomes and reports more than one statistical comparison. When many hypotheses are tested, the chance of at least one apparently unusual result can increase even if none of the underlying effects is real. Common approaches include selecting a primary comparison in advance, using a hierarchy for testing, or adjusting the threshold for multiple tests. The record does not say whether any such approach was planned or applied.

The primary p-value is unadjusted. It should therefore be understood as the result of the individual reported comparison, not necessarily as a multiplicity-adjusted test across the study’s outcomes. The registry also does not report interim analyses, data-monitoring procedures, or stopping rules. It would be inappropriate to infer that these occurred or did not occur from the final status alone.

Missing-data handling is not reported in the registry record. Although arm sizes and outcome counts are listed, the record does not clarify whether all randomized participants were assessed at the primary time point, how missing endpoint information was treated, or whether the analysis used imputation or another approach. The reported group sizes should not be assumed to establish complete follow-up. Nor does the record report the number of participants excluded from any analysis.

Analysis populations are also not described. The registry does not specify whether the primary analysis followed intention-to-treat principles, included only participants who completed treatment, or used another population definition. It does not document handling of nonadherence, treatment changes, or withdrawals. These choices can affect how a randomized comparison is interpreted, so the absence of this information limits assessment of potential bias.

These reporting gaps do not change the recorded outcome counts, but they constrain confidence in the inferential conclusions. A fuller interpretation would require the protocol or analysis plan and a report of participant flow, missingness, analysis populations, and multiplicity procedures. None of those details should be inferred from the registry summaries alone.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: proteinuria (33.0%), neutropenia (24.4%), renal allograft loss (6.5%), malignancies (4.9%).

The registry reports serious adverse events affecting 42 participants in the Control group and 117 in the Transition to Sirolimus group, with 90 and 185 participants, respectively, listed at risk. It also reports other adverse events affecting 58 participants in the Control group and 135 in the Transition to Sirolimus group. Deaths are listed as 3 in the Control group and 10 in the Transition to Sirolimus group. These are counts, and their interpretation depends on the recorded group sizes, follow-up, definitions, and completeness of reporting.

The listed serious adverse-event terms include Proteinuria at 33.0%, Neutropenia at 24.4%, Renal allograft loss at 6.5%, and Malignancies at 4.9%. The registry summary does not clarify the denominator or group-specific distribution for these term percentages, so they should not be treated as comparative rates between groups. Nor do the counts establish that a treatment caused an event. The registry does not report additional detail about event timing, severity grading, relatedness assessment, or statistical comparison of safety outcomes.

Safety counts describe what was recorded, not the full balance of risks and benefits. They should be interpreted alongside the study’s definitions and follow-up procedures, which are not fully reported in the registry record. The listed deaths are counts and do not, on their own, establish a treatment effect or explain cause.

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

The primary result is a comparison of the observed acute cellular rejection summaries in the two randomized groups at the reported assessment timeframe. The registry records more participants with rejection in the Transition to Sirolimus Group and reports a positive unadjusted risk-difference estimate with p = 0.043. This describes the direction of the posted contrast and its unadjusted statistical evidence. It does not establish that switching caused the observed difference, nor does it quantify the full clinical consequences of rejection.

The result does not show that either regimen is best for every kidney transplant recipient. The registry record does not report detailed participant characteristics or enough eligibility information to establish how representative the study population is. It also does not provide the complete analysis plan, details of adherence, or missing-data handling. Those factors matter when considering whether the result applies to people with different clinical circumstances or to care settings beyond the study.

The primary outcome should not be mistaken for a complete measure of kidney function or graft survival. The study separately lists renal allograft function, patient and graft survival, and other outcomes. Available secondary results do not answer every question listed, and the registry does not report numerical results for all of those outcomes. In particular, the primary rejection comparison does not by itself establish long-term kidney-function preservation, despite that being an interest described in the study summary.

A statistical difference and a clinically important difference are not synonymous. The p-value does not measure effect size or the probability that the finding is true. The estimated contrast and its interval provide information about magnitude and precision, but they remain dependent on the analysis method. The record does not report enough detail to judge all relevant assumptions or to determine whether the reported comparison was adjusted for other analyses.

The most defensible reading is therefore limited: the posted primary summary favors the Control group on the observed acute cellular rejection measure, and the unadjusted comparison reports p = 0.043. The findings are not a recommendation about medication choice, a comprehensive safety comparison, or proof of an effect on long-term graft outcomes. Conclusions beyond the reported endpoint and analysis would require more complete trial reporting.

17. Why This Trial Matters Statistically

This trial is statistically informative because it places a randomized medication-strategy comparison alongside a binary primary outcome and several different secondary measures. It illustrates why the event counts alone are not enough: group sizes differ, so comparisons need to account for the denominators rather than compare raw counts as if exposure were equal. The registry’s risk-difference and relative-effect summaries provide complementary scales for describing the primary contrast.

It also illustrates the distinction between statistical evidence and precision. A p-value addresses compatibility with a null comparison under test assumptions; a confidence interval communicates uncertainty about plausible effect sizes. Secondary results can differ in direction, magnitude, and precision because they measure distinct outcomes. A prominent contrast in one secondary measure is not a substitute for evidence on the primary endpoint.

The record also shows why analysis transparency matters. Without a reported statistical plan, multiplicity procedure, missing-data approach, or analysis-population definition, readers cannot fully determine how the posted comparisons relate to the trial’s intended analyses. Randomization supports a strong design in principle, but interpretation still depends on allocation implementation, follow-up, adherence, and analysis choices. The registry record documents randomization but does not give all those details.

Finally, the planning illustrations demonstrate how sample-size projections depend on the effect chosen for detection and on assumptions about allocation and statistical testing. A design based on the observed effect is not equivalent to the original trial justification and does not measure the trial’s achieved power. These distinctions are important for avoiding overconfident interpretation of a completed study’s summaries.

18. Limitations

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

The registry record leaves important trial-specific details unreported. It does not provide eligibility criteria, baseline characteristics, recruitment flow, or the criteria and procedures used to identify acute cellular rejection. Without that information, it is difficult to assess the clinical comparability of the groups at baseline, the completeness of endpoint ascertainment, or the applicability of the results to other transplant populations.

The reported primary timeframe is months 24, although assessments are listed at 6 months and 12 months as well. The record does not explain whether earlier events are included in the final count, how events were handled across visits, or how participants with incomplete follow-up were treated. It also does not describe treatment adherence, discontinuations, crossovers, or changes in immunosuppression during follow-up. These omissions limit interpretation of the randomized comparison.

The posted analyses are sparse relative to the range of listed outcomes. No sponsor analyses are recorded for the primary comparison, and the analysis plan, adjustment strategy, and analysis populations are not reported. Numerical secondary results are not reported for all listed outcomes. The record also does not give the original sample-size justification, interim-analysis details, missing-data methods, or safety-event definitions and attribution procedures.

The primary p-value is unadjusted, and the registry does not report whether multiplicity was addressed. The available group summaries support a description of the posted comparisons but do not establish that all relevant sources of uncertainty or bias have been addressed. These are limitations of the information in the registry record; they should not be filled in by assumptions about standard practice.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Conversion of Calcineurin-Inhibitors in Renal Allograft Recipients — NCT00866879.
• Registry record last updated 2019-06-28; status last verified 2019-06.
• Results first posted 2019-05-31.
• 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 record describes a completed, randomized, unmasked, parallel-group Phase 4 trial sponsored by Northwestern University. It compares continuing mycophenolate mofetil with tacrolimus against switching to mycophenolate mofetil with sirolimus after kidney transplantation. Enrollment is recorded as 275.

The primary endpoint is acute cellular rejection, reported as participants with an event at the months 24 assessment. The posted counts are 7 in the Control group and 31 in the Transition to Sirolimus Group, with an unadjusted p-value of 0.043. Secondary outcomes include renal allograft function, other health outcomes, survival, and regulatory T cells; numerical summaries are not reported for every listed outcome.

The registry does not report the original sample-size justification, detailed analysis plan, multiplicity handling, missing-data methods, or analysis populations. The posted results describe the recorded comparisons but do not resolve those uncertainties or establish conclusions beyond the outcomes and analyses documented.