Campath-1H Induction to Allow Discontinuation of Calcineurin Inhibitors After Renal Transplantation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Campath-1H Induction to Allow Discontinuation of Calcineurin Inhibitors After Renal Transplantation (NCT00214201), a randomized na study. The primary outcome is Number of Participants With Biopsy Proven Rejection.

2. Clinical Question

The trial therefore examines a treatment strategy, not simply the effect of an isolated drug exposure: withdrawal is considered in the setting of Campath-1H induction. The record does not report enough detail to reconstruct the full treatment sequence or the rules used to classify rejection. Interpretation should remain tied to the enrolled study population, the stated endpoint, and the follow-up period. The results do not automatically apply to other transplant populations, other immunosuppression strategies, or longer periods of follow-up.

3. Trial Design

The registry record describes a randomized, parallel-group trial with no masking. Enrollment was 40 participants. The two groups were labeled CNI Control Post Campath 1H and CNI Withdrawal Post Campath 1H, with 20 participants in each group for the primary endpoint. The trial status is completed. The record lists its phase as NA and identifies University of Wisconsin, Madison as the sponsor.

The recorded start was 2003-05, and primary completion was 2009-05. These are registry dates; the record does not provide a detailed account of recruitment, follow-up, or the timing of each participant’s treatment. The intervention is listed as calcineurin inhibitor withdrawal. The brief summary places this strategy after Campath-1H induction and describes the aim as assessing rejection-free renal allograft function without maintenance calcineurin inhibitor therapy.

Random allocation is intended to make treatment groups comparable, on average, with respect to factors that can affect outcomes. In a trial of this size, however, randomization does not guarantee that every prognostic characteristic will be balanced. The record does not report the sequence-generation method, concealment procedures, stratification factors, or baseline characteristics, so those design features cannot be assessed from the registry information.

No masking was recorded. Knowledge of treatment assignment can affect care, decisions about investigations, or outcome assessment, depending on the endpoint and the procedures used. The primary endpoint requires biopsy confirmation, but whether biopsy decisions and pathology assessments were conducted without knowledge of group assignment is not reported in the registry record. The original protocol, the trial’s detailed statistical plan, and its original design assumptions are also 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:

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Biopsy Proven Rejection, measured over 3 years.

The primary endpoint is the number of participants with biopsy-proven rejection during the stated 3 years. It is a binary, participant-level outcome: each participant either contributes to the count by having a qualifying rejection event or does not. The reported values are counts, rather than event rates calculated over person-time.

Biopsy confirmation gives the endpoint a specific definition: the outcome concerns rejection established by biopsy, not every possible clinical suspicion of rejection. This can make the endpoint more clinically interpretable than a broad, undefined label, but it also means the count depends on the criteria for biopsy, the decision to perform one, and the rules for classifying the findings. Those procedures and definitions are not reported in the registry record.

Rejection is used because it directly addresses the stated concern behind withdrawing maintenance calcineurin inhibitor therapy: whether participants can remain free of rejection after induction. It is still only one part of the clinical picture. A count of participants with rejection does not alone describe the severity or timing of events, other dimensions of graft function, or the overall balance of benefits and harms. The endpoint is reported over 3 years; the record does not establish what occurred after that follow-up period.

7. Results Posted in the Registry

• CNI Withdrawal Post Campath 1H: 35.0% (7/20) versus 10.0% (2/20) on control; risk difference 25.0 percentage points (95% CI 0.3 to 49.7), risk ratio 3.50 (0.83–14.83); unadjusted two-proportion z-test p = 0.058.

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.

Serum Creatinine at 36 Months (End of Study)

• 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:
  • CNI Withdrawal Post Campath 1H: mean 1.37 versus 1.49 on control; difference -0.12 (95% CI -0.38 to 0.14), standardized effect d = -0.30; z-test p = 0.365.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CNI Withdrawal Post Campath 1H and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists serum creatinine at 36 months as a secondary endpoint. This is a continuous measure, while the primary endpoint counts participants with biopsy-proven rejection. The two outcomes address related but nonidentical aspects of the transplant question: a rejection event and a laboratory measure of renal function. A pattern across them can add context, but agreement or disagreement would not make either endpoint a substitute for the other.

The secondary result should be considered alongside, rather than as a repetition of, the primary finding. A laboratory summary can help describe the groups at the recorded follow-up, but it does not establish whether rejection occurred, explain the reasons for an event, or determine the overall balance of outcomes. Conversely, the primary rejection count does not fully describe renal function. The record’s limited endpoint set cannot represent every relevant dimension of the treatment strategy.

The secondary comparison is unadjusted, and the registry record does not report a multiplicity plan or confirmatory hierarchy. When several outcomes are examined, the chance of finding an apparently notable result among them can increase. Statistical approaches to multiplicity can address that concern, but the record does not state that a particular approach was planned or used. In the absence of such information, an unadjusted secondary result carries less weight than a clearly prespecified primary comparison and should be treated as supportive or exploratory evidence.

The registry lists three outcome measures, but only one secondary endpoint is described in the posted secondary results. The other outcome details and the reasoning for which analyses were reported are not reported in the registry record. Nor does the record provide a full analysis plan that would establish whether the secondary endpoint was intended to test a distinct hypothesis or provide contextual monitoring. These gaps limit conclusions about selective reporting and about how the secondary result was meant to contribute to the study’s main question.

Overall, secondary results broaden the descriptive account but do not independently settle the primary question. They should not be used to negate, confirm, or overstate the primary comparison without a prespecified analytical framework and adequate information about completeness and uncertainty.

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

• Serum Creatinine at 36 Months (End of Study)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

A risk difference compares the proportion of participants with an event in one group with the proportion in the other. It is an absolute measure: it states the separation between the groups on the event-proportion scale. Here, the posted comparison is for calcineurin inhibitor withdrawal versus control. The estimate is 0.25, and its interval is 0.003 to 0.497. This scale can be easier to relate to the observed group counts than a relative measure, but its precision still depends on the amount of information in the trial.

The risk difference is distinct from a risk ratio or an odds ratio. A risk ratio compares event proportions as a ratio; an odds ratio compares the odds of the event. These relative measures can be useful for describing the same contrast from another perspective, but they do not convey the absolute separation in the same way. In this trial, the reported risk ratio is 3.5 with an interval from 0.826 to 14.83, and the reported odds ratio is 4.846 with an interval from 0.863 to 27.22. The intervals are broad, so the relative estimates also have substantial uncertainty.

What does an unadjusted p-value tell the reader?

A p-value measures how unusual data at least as incompatible with a null model as the observed data would be, assuming that model and the analysis conditions. It is not the chance that the treatment groups are truly identical, nor is it a measure of the probability that the observed result arose by chance in a general sense. The posted unadjusted p-value for the primary comparison is 0.058. It should be interpreted alongside the effect estimate and interval rather than used as a stand-alone decision rule.

Unadjusted means the posted comparison is not described as controlling for other variables. An adjusted analysis can account for specified covariates, but the covariates, model, and adjusted results are not reported in the registry record. The registry record also does not report a prespecified statistical testing threshold or a complete analysis plan. Consequently, it is not possible to establish from the record whether the posted comparison follows the original planned analysis.

Why are confidence intervals important?

A confidence interval gives a range of estimates compatible with the data under the method used. In general, an interval is more informative than a point estimate alone because it displays the uncertainty in the estimated effect and the range of effect sizes that remain plausible under that method. A narrow interval indicates greater precision than a wide interval, though precision does not determine clinical importance or eliminate bias.

The primary risk-difference interval extends from 0.003 to 0.497. Its breadth means that the data do not locate the size of the group difference precisely. The confidence level and interval calculation procedure are not reported in the registry record, so those methodological details should not be assumed. The risk-ratio and odds-ratio intervals are also broad. Their ranges convey uncertainty on relative scales and should not be substituted for the absolute comparison.

Why can small event counts make estimates unstable?

With binary outcomes, the analysis depends on how many participants in each group experienced the event and how many were observed. When the groups and event counts are limited, a small change in the observed count can change the estimated contrast appreciably. This is one reason to consider the interval and the underlying counts together. The group counts are 2 of 20 in control and 7 of 20 in withdrawal; they are the observed data, not a guarantee of the event proportions that would occur in a larger study.

Randomization supports a fair comparison by assigning participants to groups without choosing treatment based on their characteristics. It does not ensure perfect balance in a small sample, and it cannot address problems such as incomplete outcome ascertainment or departures from the assigned strategy. The allocation method beyond the description randomized, the handling of deviations, and the analysis population are not reported in the registry record.

What is the role of the continuous secondary measure?

Serum creatinine is reported as a mean with a standard deviation for each group at 36 months. A mean summarizes the central value of a continuous measurement, while a standard deviation describes variability among measured values. The mean-difference comparison is a contrast between group averages, not a count of participants with an event. It therefore answers a related but distinct question from the primary binary endpoint.

The registry reports an unadjusted secondary comparison and no reported analyses beyond the posted summaries. Without a stated analysis plan, details about missing measurements, or a multiplicity approach, the secondary result should be interpreted cautiously. General statistical practice treats multiple unadjusted outcomes as exploratory unless the plan specifies how they are to support confirmatory claims. That general principle does not establish what the investigators intended in this trial; their intention is not reported in the registry record.

What can the registry summaries establish?

The summaries describe the observed group outcomes and give unadjusted comparisons with uncertainty estimates. They do not reveal all the information needed to reproduce a full trial analysis. The registry record does not report the original protocol’s statistical methods, the approach to missing observations, the handling of protocol deviations, or the analysis populations. These omissions limit assessment of whether the posted comparisons were prespecified and whether all randomized participants were included as intended.

Statistical evidence should therefore be read in layers: the observed counts and measurements, the estimated group contrasts, their uncertainty, and the completeness of the analysis description. No single layer answers every clinical or methodological question. The posted results support a description of what was recorded in the two groups; they do not, by themselves, resolve uncertainty about treatment effects beyond this trial.

11. Confidence Intervals and Precision

Precision concerns how closely an estimate locates the underlying group contrast. The primary risk-difference estimate is 0.25, with an interval from 0.003 to 0.497. This wide span indicates that the size of the absolute difference is not estimated closely. The lower end is near zero, while the upper end allows a much larger difference. Thus, the point estimate should not be read as if it were known without substantial uncertainty.

The reported relative comparisons are similarly imprecise. The risk ratio is 3.5, with an interval from 0.826 to 14.83, and the odds ratio is 4.846, with an interval from 0.863 to 27.22. The intervals include values on both sides of the respective no-difference values. The data therefore do not pin down the relative effect with precision. Relative and absolute measures emphasize different scales, so neither should be interpreted in isolation.

A confidence interval is generally a range generated by a statistical procedure that reflects sampling uncertainty under its assumptions. It is not a guarantee that the true effect lies in the interval, and it does not account automatically for bias, missing data, measurement problems, or an unsuitable analysis. The confidence level and exact interval method are not reported in the registry record, so the intervals should be read as posted estimates without attributing an unreported procedure to them.

The primary endpoint groups each contain 20 participants, and the recorded event counts are 2 and 7. Limited information can result in wide uncertainty, particularly for comparisons based on event counts. The secondary endpoint also has fewer measured participants than the primary endpoint groups: 18 per group are reported for serum creatinine. The registry record does not explain why those endpoint counts differ or how unavailable observations were handled. The estimates are therefore best understood as descriptive comparisons with notable uncertainty, not precise forecasts of results in other settings.

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 estimates are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these non-time-to-event outcomes, the figures are participants per arm, not total events. The calculations assume 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 sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under which the calculation would have an 80% chance of detecting the specified effect, if the assumptions and effect were correct. The 90% power column uses a higher target chance of detection and therefore calls for more participants under the same planning framework. These are planning concepts, not guarantees that a future study will detect an effect.

The estimates are displayed for planning at 100%, 75%, and 50% of the observed effect. The smaller the effect targeted for detection, the more participants are needed under the stated assumptions. This pattern is expected because a smaller separation between groups is harder to distinguish from sampling variation. The figures should not be treated as recommendations for a future trial without a new design assessment, including a justified target effect and suitable assumptions.

This is not observed power. It is a forward-looking illustration calculated from the observed effect and stated planning assumptions; it does not describe the probability that this completed trial’s result is correct. In particular, using an effect estimated from a small trial can produce planning figures that are sensitive to uncertainty in that estimate. The registry record does not report the original sample-size rationale, so the illustration should not be mistaken for evidence about how the investigators planned the trial.

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 = 0.100; treatment proportion p₁ = 0.350; average p̄ = 0.225.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5906 = 1.1575.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5635 = 0.4742.
4. n = (1.1575 + 0.4742)² / (0.2500)² = 42.6, rounded up to 43 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 <- 0.1                          # control proportion
p1 <- 0.35                          # 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(214201)
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 = 43 (80% power), 57 (90% power)
 75% of observed effect: n per arm = 69 (80% power), 92 (90% power)
 50% of observed effect: n per arm = 136 (80% power), 181 (90% power)
power.prop.test: 42.6 
Simulated power at n = 43 per arm: 0.831 (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 a multiplicity strategy. Multiplicity arises when several outcomes, comparisons, time points, or subgroup analyses are examined. If each is tested separately without accounting for the number of opportunities to find a result, the chance of at least one apparently unusual finding can increase. This general concern does not prove that a false positive occurred in this trial; it explains why unadjusted secondary findings require caution.

The record identifies a primary endpoint and one secondary endpoint in the posted outcome results, while listing three outcome measures overall. It does not report a hierarchy for testing, a family of hypotheses, or any adjustment of p-values or confidence intervals for multiple testing. The original statistical analysis plan is not reported in the registry record. It is therefore not possible to determine whether the posted endpoint comparisons were the complete set of planned analyses or whether a multiplicity approach was specified elsewhere.

Information about missing data is also limited. The primary endpoint summaries list 20 participants per group, and the serum creatinine summaries list 18 per group. The registry record does not report why these denominators differ, whether measurements were missing, how missing outcomes were handled, or whether participants were excluded from any analysis. The difference in listed denominators should not be interpreted as proof of a particular reason for missingness.

The analysis populations are not reported in the registry record. In particular, the record does not state whether the primary comparison included all randomized participants according to their assigned groups, or whether any other population was used. It also does not report how treatment changes, withdrawals, or protocol deviations were handled. These details matter because estimates can depend on who is included and how outcomes are classified.

The registry lists no reported analyses beyond the posted summaries. This limits the ability to assess adjusted estimates, sensitivity analyses, subgroup results, or checks of assumptions. The omissions do not establish that these procedures were never conducted; they mean that their methods and results are not reported in the registry record. Interpretation should therefore remain limited to the posted unadjusted comparisons and the outcome counts described.

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: hydronephrosis (15.0%), kidney transplant rejection (10.0%), cytomegalovirus (10.0%), chronic obstructive pulmonary disease (10.0%), atrial fibrillaiton (5.0%).

The serious adverse event summary reports 11 affected participants among 20 at risk in the control group and 8 among 20 at risk in the withdrawal group. These are group-level counts of participants affected, not counts of every event episode. The registry record also lists other adverse events: 10 affected among 20 at risk in control and 11 among 20 at risk in withdrawal. The definitions, collection procedures, and follow-up details for these summaries are not reported in the registry record.

The listed serious event terms include hydronephrosis, kidney transplant rejection, cytomegalovirus, Chronic Obstructive Pulmonary Disease, Atrial Fibrillaiton, and encephalitis, with percentages attached to the terms in the registry. The list is not identified by treatment group in the posted summary, so the terms should not be attributed to one arm or used to compare arm-specific risk. The registry record does not report the basis used for those percentages or provide a full account of all event terms.

Deaths are not reported in the registry record. Counts of participants with reported events describe what was recorded; by themselves, they do not establish that an event was caused by treatment or that the groups had equivalent safety. No medical conclusion should be drawn from these limited summaries without fuller definitions, ascertainment details, and context.

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

The primary comparison shows more participants with biopsy-proven rejection in the calcineurin inhibitor withdrawal group than in the control group during the stated 3-year period. The estimated risk difference is 0.25, but its interval is broad, from 0.003 to 0.497. The unadjusted p-value is 0.058. Taken together, these results describe an observed difference while also showing substantial uncertainty about its size. They do not provide a precise estimate of what would be expected in a different set of participants.

The result does not establish a causal explanation for every rejection event, nor does it show that treatment assignment alone accounts for all observed differences. Randomization is an important design feature, but interpretation also depends on complete follow-up, outcome assessment, and analysis choices. The registry record does not report enough detail to evaluate all of these features. The relative estimates are imprecise as well, and should not be read as stable measures of effect.

The result also does not determine the overall balance of outcomes. The primary endpoint is a count of participants with biopsy-proven rejection. The secondary endpoint measures serum creatinine, and the adverse-event summaries provide limited safety context. These outcomes are not interchangeable, and the record does not report a comprehensive analysis that combines them into an overall assessment. The presence of a secondary measure cannot by itself confirm or overturn the primary comparison.

Nor does the record establish what happens beyond the stated follow-up, in other transplant populations, or under different induction and maintenance strategies. The eligibility criteria, detailed treatment procedures, and broader applicability information are not reported in the registry record. The findings should therefore be understood in the context of this completed randomized comparison, its recorded endpoints, and its limited posted analysis details.

In plain terms, the posted data show a higher observed count of biopsy-proven rejection in the withdrawal group, alongside considerable uncertainty and incomplete reporting of key analysis details. This supports a cautious description of the trial results, not a definitive claim about treatment effects or a medical recommendation.

17. Why This Trial Matters Statistically

This trial is statistically informative because it makes the contrast explicit: calcineurin inhibitor withdrawal after Campath-1H induction is compared with continued calcineurin inhibitor immunosuppression after induction. Randomization gives the comparison a design intended to reduce systematic differences between groups. The results then show why design quality and estimate precision must be considered together: a randomized comparison can still yield uncertain estimates when the number of participants and observed events is limited.

The primary endpoint is expressed as a participant count and an absolute risk difference, with relative measures also reported. Looking across these scales helps distinguish the observed absolute separation from the relative comparison. Here, all of the effect summaries need cautious interpretation because their intervals are broad. The point estimate alone would conceal that uncertainty, while a p-value alone would not communicate the range of effect sizes compatible with the analysis.

The trial also illustrates why endpoint distinctions matter. Biopsy-proven rejection and serum creatinine are related to the transplant question but capture different outcomes. A coherent interpretation cannot treat one as a replacement for the other. Likewise, adverse event summaries are important context, but the limited group-level reporting and lack of detail about event attribution do not support a comprehensive safety comparison.

Finally, the registry record exposes important limits on secondary interpretation: the original statistical plan, analysis populations, missing-data procedures, and multiplicity approach are not reported. Those details determine how much confidence readers can place in the completeness and prespecification of the posted analyses. The study is therefore a useful example of reading results through both the numerical estimates and the reporting context, rather than treating any single statistic as conclusive.

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 specific to this trial constrain interpretation. The primary endpoint groups contain 20 participants each, and the event counts are 2 and 7. With limited observations, the estimated difference is vulnerable to sampling variation, as reflected in the broad intervals. The trial therefore provides an imprecise estimate of the magnitude of the observed group contrast.

The registry describes the study as randomized and unmasked, but does not report the randomization procedures, concealment methods, or whether biopsy decisions and pathology assessments were made without knowledge of group assignment. Because the primary endpoint depends on biopsy confirmation, information about how and when biopsies were performed would help assess ascertainment. These details are not reported in the registry record.

The record also does not provide detailed eligibility criteria, baseline participant characteristics, the treatment schedule, or rules for withdrawal and other deviations. It is not possible to assess group comparability on recorded baseline variables or to understand precisely how the treatment strategies were implemented. Generalizability to participants outside the enrolled primary renal transplant population cannot be established from the posted information.

Analysis reporting is limited. The original statistical plan, analysis populations, missing-data methods, and multiplicity procedures are not reported in the registry record. The primary endpoint lists 20 participants in each group, while the secondary endpoint lists 18 in each group; the record does not explain the different denominators. The posted summaries do not establish whether all randomized participants were included in each analysis or how unavailable measurements were handled.

Follow-up for the primary endpoint is stated as 3 years, and the secondary measure is recorded at 36 months +/- 60 days. The record does not supply detailed follow-up completeness or longer-term outcomes. Serious adverse event reporting is also limited: deaths are not reported in the registry record, and the listed serious event terms are not presented as arm-specific. These gaps mean that the findings are best read as a narrow description of the posted outcomes, rather than a complete account of efficacy, safety, or long-term transplant outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Campath-1H Induction to Allow Discontinuation of Calcineurin Inhibitors After Renal Transplantation — NCT00214201.
• Registry record last updated 2012-10-03; status last verified 2012-09.
• Results first posted 2012-09-12.
• 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

NCT00214201 is a completed, randomized, parallel-group trial with no masking, sponsored by University of Wisconsin, Madison. The registry lists 40 enrolled participants with primary renal transplantation and records the phase as NA. The comparison was calcineurin inhibitor withdrawal after Campath-1H induction versus standard-of-care calcineurin inhibitor immunosuppression after induction.

The primary endpoint was the number of participants with biopsy-proven rejection over 3 years. The recorded counts were 2 of 20 in control and 7 of 20 in withdrawal. The unadjusted risk difference was 0.25, with an interval from 0.003 to 0.497, and the unadjusted p-value was 0.058. Serum creatinine at 36 months was the listed secondary endpoint. Serious and other adverse event summaries were also posted.

The estimates are imprecise, and details about the original statistical plan, analysis populations, missing data, and multiplicity are not reported in the registry record. The results describe the posted trial outcomes and should be interpreted in that context.