A Study to Assess the Efficacy and Safety of Alefacept in Kidney Transplant Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Efficacy and Safety of Alefacept in Kidney Transplant Recipients (NCT00617604), a randomized phase 2 study. The primary outcome is Percentage of Participants With Biopsy-confirmed Acute T-cell Mediated Rejection at Month 6 Assessed by Local Review.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, placebo-controlled Phase 2 study of alefacept in de novo kidney transplantation. The official title describes the study as multicenter, double-blind and placebo controlled; the registry record also lists quadruple masking. Enrollment was 218, and the record lists the study status as completed. The recorded start was 2007-12 and primary completion was 2009-09.

The two groups received the same background treatment of tacrolimus, mycophenolate mofetil and steroids. The experimental group also received alefacept, while the comparison group received placebo. Alefacept was administered intra-operatively as an intravenous bolus on Day 0, with another bolus on Day 3, followed by weekly subcutaneous injections for 12 weeks. The placebo schedule followed the same administration pattern.

The primary endpoint population is described as the full analysis set: all randomized and transplanted participants who received at least 1 dose of study drug. The reported group denominators for this endpoint were 107 for placebo and 105 for alefacept. The record does not report the original sample-size justification or the trial's planned statistical assumptions. It also does not report the method used to generate the random sequence or details of how allocation was concealed.

The primary outcome was assessed at Month 6. The study also listed secondary outcomes concerning antibody-mediated, T-cell mediated, mixed and clinically diagnosed acute rejection, as well as patient survival. The registry record lists 20 outcome measures and 14 analyses. Those counts alone do not establish which outcomes were prespecified as confirmatory or how the investigators prioritized them.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (all randomized and transplanted participants who received at least 1 dose of study drug)

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: All randomized patients who took at least 1 dose of study drug (Safety Analysis Set).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Biopsy-confirmed Acute T-cell Mediated Rejection at Month 6 Assessed by Local Review, measured over 6 months.

The primary endpoint was the percentage of participants with biopsy-confirmed acute T-cell mediated rejection by Month 6, assessed by local review. The registry record describes biopsies graded by the clinical site pathologist using the Banff 97/05 updated histological classification. A suspected acute rejection counted as an event when a graft biopsy confirmed rejection at Banff grade 1 or higher.

This endpoint captures a rejection event supported by tissue assessment, rather than relying only on symptoms or treatment decisions. Biopsy confirmation can make the outcome more clinically specific, while the local-review approach means the assessment was made at the clinical site. The record also lists a secondary outcome assessed by central review, but the primary result is the local-review endpoint.

The registry describes the primary result as a Kaplan-Meier estimate of rejection within the first 6 months following transplantation. Participants lost to follow-up or with missing outcomes were censored at their last follow-up visit. In general, a time-to-event estimate uses both whether an event occurred and when it occurred, while censoring allows follow-up information up to the last known visit to contribute without treating the unobserved period as event-free. The endpoint is therefore not simply a comparison of raw percentages without regard to follow-up timing.

The primary outcome is useful for focusing the comparison on biopsy-confirmed acute T-cell mediated rejection during the stated follow-up window. It does not, by itself, describe every form of rejection, graft function, patient survival, or the overall balance of benefits and harms.

7. Results Posted in the Registry

• Alefacept: 10.5% (11/105) versus 6.5% (7/107) on control; risk difference 3.9 percentage points (95% CI -3.6 to 11.4), risk ratio 1.60 (0.65–3.97); unadjusted two-proportion z-test p = 0.304.

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.

Percentage of Participants With Biopsy Confirmed Antibody-Mediated Acute Rejection at Month 6

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Alefacept: 3.8% (4/105) versus 2.8% (3/107) on control; risk difference 1.0 percentage points (95% CI -3.8 to 5.8), risk ratio 1.36 (0.31–5.92); unadjusted two-proportion z-test p = 0.682.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Alefacept and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Biopsy Confirmed Acute Rejection (T-Cell Mediated or Antibody Mediated) at Month 6

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Alefacept: 12.4% (13/105) versus 9.3% (10/107) on control; risk difference 3.0 percentage points (95% CI -5.3 to 11.4), risk ratio 1.32 (0.61–2.89); unadjusted two-proportion z-test p = 0.477.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Alefacept and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Biopsy Confirmed Acute Mixed T-Cell Mediated and Antibody-Mediated Rejection at Month 6

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Alefacept: 1.0% (1/105) versus 0.0% (0/107) on control; risk difference 1.0 percentage points (95% CI -0.9 to 2.8); unadjusted two-proportion z-test p = 0.312.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Alefacept and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several related but distinct ways of describing rejection, including antibody-mediated rejection, combined T-cell mediated or antibody-mediated rejection, mixed rejection, clinically diagnosed rejection, steroid-resistant rejection and central review of T-cell mediated rejection. Patient survival is also listed. This broader set gives clinical context around the primary endpoint, but the outcomes are not interchangeable: they differ in how events are defined, detected or assessed.

The posted secondary estimates show a varied pattern rather than a consistent separation in one direction across all outcomes. For the secondary endpoints with comparisons, the uncertainty intervals include zero. This is compatible with the imprecision seen for the primary endpoint. It does not establish that every outcome has the same underlying effect, and it does not convert the primary result into evidence of no effect.

Secondary outcomes can help describe the trial, but multiple comparisons raise the chance that at least one result may appear notable by chance when many endpoints are examined. The registry record lists 19 secondary outcomes as posted and 14 analyses, but does not report a multiplicity adjustment or a hierarchy that identifies confirmatory secondary tests. The secondary results should therefore be interpreted as exploratory or descriptive unless the analysis plan establishes otherwise; that plan is not reported in the registry record.

Because the definitions and assessment methods differ, the secondary outcomes should be considered alongside the primary endpoint rather than combined into an informal overall score. Their role is to provide additional context, not to override the uncertainty in the primary comparison. The registry record does not provide enough detail to determine how missing results, multiplicity or prespecification were handled for every secondary analysis.

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

• Percentage of Participants With Biopsy Confirmed Antibody-Mediated Acute Rejection at Month 6
• Percentage of Participants With Biopsy Confirmed Acute Rejection (T-Cell Mediated or Antibody Mediated) at Month 6
• Percentage of Participants With Biopsy Confirmed Acute Mixed T-Cell Mediated and Antibody-Mediated Rejection at Month 6
• Percentage of Participants With Acute Rejection Diagnosed by Signs and Symptoms at Month 6
• Percentage of Participants With Clinically Treated Acute Rejection at Month 6
• Percentage of Participants With Steroid-resistant Acute Rejection at Month 6
• Percentage of Participants With Biopsy-Confirmed Acute T-cell Mediated Rejection as Assessed by Central Review at Month 6
• Patient Survival

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared?

The primary endpoint is binary at the participant level: a participant either has a biopsy-confirmed acute T-cell mediated rejection event during the stated period or does not. A group percentage summarizes how often the endpoint was observed or estimated in that group. The direct comparison is an absolute difference in event risk, rather than a relative measure such as a risk ratio. An absolute difference is often easier to relate to the underlying event percentages, but it remains an estimate subject to sampling uncertainty.

Random allocation is intended to make treatment groups comparable, on average, with respect to measured and unmeasured characteristics. It does not guarantee that every feature will be balanced in a particular study. Blinding can reduce the influence of knowledge of assigned treatment on care, assessment or reporting. The registry record describes the design as quadruple masked and the official title describes it as double-blind. The record does not specify which roles were included in each masking description, so no more detailed account of masking can be inferred.

Why use a time-to-event estimate?

The registry describes a Kaplan-Meier estimate of biopsy-confirmed rejection within the first 6 months after transplantation. In general, Kaplan-Meier methods estimate the event experience over time and allow participants with incomplete follow-up to contribute information until their last observed time. Censoring means that follow-up ends without a recorded event at that point; it does not establish that an event would never occur after that time.

For this endpoint, the record says that participants lost to follow-up or with missing outcomes were censored at their last follow-up visit. This is a stated handling rule, but it does not reveal how many participants were censored, why particular outcomes were missing, or whether the censoring assumptions were assessed. Those details are not reported in the registry record.

How should the risk difference and p-value be read?

The recalculated risk difference is a simple unadjusted comparison based on the posted summary counts. The estimate is 0.039, and the interval is -0.036 to 0.114. These values are on the proportion scale. The unadjusted p-value is 0.304. A p-value measures how compatible the observed data are with a specified null model, assuming that model and the analysis assumptions are appropriate. 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 recalculation is not the same as the sponsor's endpoint analysis simply because both concern the same outcome. In general, a calculation based on aggregate counts may not preserve the timing and censoring information used by a time-to-event method. The sponsor's reported analysis gives a difference of 3.9 with a 90% confidence interval from -2.5 to 10.3. The record does not describe the specific method behind that reported contrast. The registry record's analysis is therefore important context when interpreting the recalculation.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the observed data under a particular statistical procedure. Narrower intervals indicate greater precision, while wider intervals indicate greater uncertainty. An interval that includes zero for a difference does not show that the groups are identical; it indicates that the data do not rule out no difference at the interval's stated confidence level. It can also include nonzero differences, which should be considered when judging how much uncertainty remains.

The primary result includes a 90% confidence interval for the sponsor-reported difference. The arm estimates also have 90% confidence intervals. The recalculated interval is presented as a simple unadjusted recalculation; its confidence level is not separately stated in the registry record. These intervals should not be treated as interchangeable when they arise from different analyses or assumptions.

Why can over-dispersion matter?

Over-dispersion is a general issue that can arise when observed outcomes vary more than a statistical model expects. In count or rate analyses, ignoring over-dispersion can make uncertainty appear too small. The primary outcome is a binary event and the registry describes a Kaplan-Meier estimate, so over-dispersion is not identified as a feature of the reported primary method. It would not be appropriate to assume that an over-dispersion adjustment was used.

What is not specified?

The registry record does not report the full statistical analysis plan, the original sample-size justification, the randomization procedure, or any interim analysis plan. It also does not state whether the primary analysis adjusted for baseline factors or how multiplicity across outcomes was handled. Those omissions limit what can be inferred about prespecification and confirmatory testing. General statistical concepts can explain what these methods would do, but they cannot establish that the study used them.

11. Confidence Intervals and Precision

The group estimates for the primary endpoint are 6.7% for placebo and 10.6% for alefacept. Their 90% confidence intervals, 2.7% to 10.7% and 5.6% to 15.6%, respectively, convey uncertainty around those estimates. The considerable overlap between the ranges is consistent with the uncertainty in the between-group comparison, although overlap or non-overlap of separate group intervals is not itself a formal test of a difference.

The sponsor-reported difference is 3.9 percentage points, with a 90% confidence interval from -2.5 to 10.3 percentage points. Because the interval crosses zero, the data are compatible with no difference as well as with differences in either direction. Its width means that the result does not pin down the size or direction of the underlying effect with high precision.

In general, confidence intervals communicate both the estimated effect and its uncertainty, which a single p-value cannot do. A narrow interval can support a more precise estimate; a wide interval leaves more plausible values unresolved. The primary interval does not provide a basis for declaring equivalence, because no equivalence margin is reported. Nor does the fact that a confidence interval includes zero prove that the treatments have identical effects.

The recalculated interval from posted summaries is -0.036 to 0.114 around a risk difference of 0.039. It is an unadjusted recalculation and should be distinguished from the sponsor's reported difference and interval. The primary outcome's stated Kaplan-Meier approach includes follow-up time and censoring, while a simple summary-count calculation does not necessarily represent that analysis. The registry record does not report enough detail to reconcile the interval methods fully.

Precision is also tied to the amount of endpoint information, not merely the enrollment figure. The primary outcome population is specified, but details about censoring and missing results are not reported. Consequently, the displayed intervals should be read as uncertainty estimates under their respective analyses, not as a complete account of every source of uncertainty in the trial.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design calculation. For this binary outcome, the figures are participants per arm, not total events. The planning assumptions listed in the registry-derived analysis 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 as the stated fraction of the observed effect.

The 80% power column describes the planned number of participants per arm under those assumptions for a hypothetical study with an 80% chance of detecting the specified effect if that effect is real and the assumptions hold. The 90% power column uses a higher chance of detection and therefore requires more participants per arm under the same assumptions. These are planning concepts, not descriptions of what happened in this completed trial.

For the primary endpoint, planning for 100% of the observed effect gives 789 participants per arm for 80% power and 1,055 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,329 participants per arm for 80% power and 1,779 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,823 participants per arm for 80% power and 3,778 participants per arm for 90% power. The pattern illustrates the general principle that smaller effects require more participants to detect, all else being equal.

This is not observed power. It is a forward-looking planning illustration constructed from the observed effect; it does not show the probability that the completed trial successfully detected an effect. The original trial's sample-size assumptions and justification are not reported in the registry record, so these figures should not be read as a reconstruction of the investigators' original plan.

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 = 0.065; treatment proportion p₁ = 0.105; average p̄ = 0.085.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3946 = 0.7734.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3936 = 0.3313.
4. n = (0.7734 + 0.3313)² / (0.0393)² = 788.4, rounded up to 789 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 <- 0.0654205607476635                          # control proportion
p1 <- 0.104761904761905                          # 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(617604)
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 = 789 (80% power), 1,055 (90% power)
 75% of observed effect: n per arm = 1,329 (80% power), 1,779 (90% power)
 50% of observed effect: n per arm = 2,823 (80% power), 3,778 (90% power)
power.prop.test: 788.4 
Simulated power at n = 789 per arm: 0.801 (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 sponsor-reported primary comparison is a difference of 3.9 percentage points, with a 90% confidence interval from -2.5 to 10.3 percentage points. The interval includes zero, so the reported analysis does not establish a statistically clear difference between groups. The registry record does not include a p-value for this sponsor-reported contrast.

The unadjusted recalculation from the posted summary counts gives a risk difference of 0.039, with an interval from -0.036 to 0.114, and an unadjusted p-value of 0.304. This is a simple recalculation from aggregate summaries, while the endpoint description identifies a Kaplan-Meier estimate and censoring rule. The recalculated values should be treated as a separate, unadjusted analysis rather than as a replacement for the sponsor's analysis.

The registry record marks no discrepancy between the reported and recalculated results. Even so, the analyses are not identical in their stated basis, and the sponsor's reported analysis is the relevant analysis for the trial's own endpoint reporting. The posted information does not describe enough about the sponsor's calculation to explain all methodological details or to make a stronger claim about why the intervals differ in form.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 20 outcome measures and 14 analyses, and 19 secondary outcomes are posted. Testing or estimating many outcomes creates a multiplicity issue: when several hypotheses are examined, the chance of at least one apparently notable result can increase even if there is no genuine effect on any outcome. In general, investigators may address this through a prespecified hierarchy, adjustment procedures, or by labeling secondary analyses as exploratory. The registry record does not report which approach, if any, was used.

The record does not report whether the primary endpoint was the only confirmatory analysis, whether any interim analyses were planned or conducted, or whether adjustments were made for multiple comparisons. The number of posted outcomes alone cannot answer those questions. The unadjusted p-value from the summary-count recalculation should not be interpreted as multiplicity-adjusted evidence.

The primary endpoint population is described as all randomized and transplanted participants who received at least 1 dose of study drug. This is the registry's stated full analysis set, not a general intention-to-treat description that can be extended to participants outside that definition. The record does not provide a separate per-protocol population or a detailed account of exclusions after randomization.

For the primary endpoint, participants lost to follow-up or with missing outcomes were censored at their last follow-up visit. This specifies how those cases entered the Kaplan-Meier estimate, but the number of affected participants, reasons for missingness and sensitivity analyses are not reported in the registry record. Censoring relies on assumptions about the relationship between the end of observed follow-up and the chance of an event. The record does not describe whether those assumptions were examined.

The original sample-size justification, analysis plan and details of any interim monitoring are also not reported in the registry record. Their absence limits evaluation of whether the primary analysis, outcome hierarchy and missing-data handling followed prespecified procedures.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: histology abnormal (10.3%), cytomegalovirus infection (8.6%), complications of transplanted kidney (7.6%), bk virus infection (7.5%), renal impairment (7.5%).

The serious adverse event figures describe participants with at least one serious adverse event within each reported group: 62 of 107 in the placebo group and 57 of 105 in the alefacept group. The figures for participants with other adverse events are 98 of 107 for placebo and 92 of 105 for alefacept. These counts are descriptive and do not, by themselves, establish that the groups differ in safety.

The registry record lists serious adverse event terms including Histology abnormal at 10.3%, Cytomegalovirus infection at 8.6%, Complications of transplanted kidney at 7.6%, Bk virus infection at 7.5%, Renal impairment at 7.5% and Urinary tract infection at 5.6%. These are listed as top serious terms; the record does not attach these percentages to a particular treatment group in the information. They should not be interpreted as comparative treatment-specific rates.

Deaths are not reported in the registry record. The posted summary does not give enough detail to assess event timing, duration, severity gradation beyond the serious-event classification, or whether events were considered related to treatment. Safety interpretation therefore remains descriptive and should be made alongside the efficacy endpoints and the limits of the reported safety detail.

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

The primary result describes biopsy-confirmed acute T-cell mediated rejection by Month 6 in the registry-defined full analysis set. The estimates were 6.7% for placebo and 10.6% for alefacept, with uncertainty around both group estimates. The sponsor-reported difference was 3.9 percentage points, and its 90% confidence interval ranged from -2.5 to 10.3 percentage points.

That interval includes zero and spans values on either side of no difference. The data therefore do not provide a precise estimate of the direction or size of a difference. This is not proof that the strategies are identical, and it is not evidence of equivalence. The record does not report an equivalence or non-inferiority design or margin.

The result is specific to the study population, background treatment, alefacept and placebo schedules, local-review biopsy endpoint, and Month 6 timeframe. It does not establish what would happen with other transplant populations, treatment regimens, outcome definitions or follow-up periods. The trial was a Phase 2 study, and the registry record does not provide the full protocol or statistical analysis plan needed to assess every design and analysis choice.

The secondary outcomes add information about other rejection definitions and patient survival, but their interpretation is limited by uncertainty and the absence of a reported multiplicity strategy. Safety counts are also descriptive and do not establish comparative risk. A full assessment would consider the endpoint findings, safety information, follow-up and the broader clinical context together; the registry record alone does not answer every question about the treatment strategies.

In statistical terms, the most defensible reading is that the posted comparison is inconclusive about a clear between-group difference in the primary endpoint. The evidence is not sufficiently precise to rule out all potentially important differences. It should not be translated into medical advice or a claim that alefacept does or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated effect should be read together with its confidence interval. The point estimates differ, but the sponsor-reported interval spans no difference and effects in either direction. Reporting the estimate alone could overstate certainty; focusing only on whether an interval crosses zero could also hide how much uncertainty remains.

It also highlights that the analysis method matters. The primary outcome is described as a Kaplan-Meier estimate with censoring for participants lost to follow-up or with missing outcomes. A simple recalculation from aggregate counts is useful as a check on the posted summaries, but it does not necessarily preserve timing and censoring. It should not silently replace the endpoint analysis reported by the sponsor.

The trial includes multiple secondary outcomes addressing related but non-identical definitions of rejection. Without a reported hierarchy or multiplicity approach, those results need cautious interpretation. More outcomes do not automatically create stronger evidence; they can create more opportunities for chance findings while also offering useful descriptive context.

Finally, the planning illustration makes clear that sample-size requirements depend on the effect a future study aims to detect. Smaller target effects generally require more participants under the stated assumptions. Those illustrations are distinct from the study's original design justification, which is not reported in the registry record. Together, these features show how endpoint choice, analysis methods, precision, multiplicity and planning assumptions shape the interpretation of a clinical trial.

19. Limitations

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

The registry record does not report the original sample-size justification, so the enrollment cannot be evaluated against a documented target effect or planned precision. The planning figures based on the observed effect are not a substitute for that missing design information.

The primary endpoint description specifies local pathology review and a Kaplan-Meier estimate, but the record does not give the number of censored participants, the amount of missing outcome data, or sensitivity analyses for censoring assumptions. It also does not report enough detail about the sponsor's statistical method to fully reconcile its result with an unadjusted calculation from summary counts.

Multiplicity handling is not reported despite the presence of numerous secondary outcomes. Without a reported hierarchy or adjustment, secondary findings should be treated cautiously. The record also does not specify whether any interim analyses occurred, whether baseline adjustment was used, or what randomization and allocation-concealment procedures were followed.

The safety summary gives counts of participants with serious and other adverse events, but it does not report event timing, treatment attribution or detailed comparative analyses. The listed serious-event terms are not clearly allocated by treatment group in the record information presented, and deaths are not reported in the registry record.

Finally, the primary endpoint is limited to biopsy-confirmed acute T-cell mediated rejection within the stated follow-up window. It does not capture every clinically relevant outcome after transplantation. These limitations constrain the conclusions that can be drawn from the registry results without additional trial documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Assess the Efficacy and Safety of Alefacept in Kidney Transplant Recipients — NCT00617604.
• Registry record last updated 2016-02-04; status last verified 2016-01.
• Results first posted 2016-02-04.
• 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

NCT00617604 is a completed randomized, parallel-group, placebo-controlled Phase 2 study of alefacept in de novo kidney transplantation. The intervention was added to tacrolimus, mycophenolate mofetil and steroids; the comparison group received placebo with background immunosuppressive treatment. Enrollment was 218.

The primary endpoint was biopsy-confirmed acute T-cell mediated rejection by Month 6, assessed by local review. The sponsor-reported difference was 3.9 percentage points, with a 90% confidence interval from -2.5 to 10.3. The interval includes no difference and leaves substantial uncertainty about the direction and magnitude of the comparison.

The registry record lists multiple secondary rejection outcomes and safety summaries, but does not report the full statistical analysis plan, multiplicity approach, original sample-size justification or detailed missing-data information. The posted findings are best read as an uncertain comparison rather than a definitive conclusion about treatment effect.