To Compare the Effects of Immediate-release Tacrolimus and Astagraf XL on Donor-Specific Antibody (DSA) Formation and the Development of Immune Activation (IA) in de Novo Kidney Transplant Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Compare the Effects of Immediate-release Tacrolimus and Astagraf XL on Donor-Specific Antibody (DSA) Formation and the Development of Immune Activation (IA) in de Novo Kidney Transplant Recipients (NCT02723591), a randomized phase 4 study. The primary outcome is Percentage of Participants Who Were Positive for de Novo DSA (dnDSA) or Immune Activation (IA) Occurrence.

2. Clinical Question

The clinical question concerns the comparative frequency of a composite outcome, not a direct measure of graft function or survival. The composite counts either of its two components: de novo DSA formation or an IA designation. A participant could therefore meet the outcome through either pathway. The registry describes DSA as a binary measure and IA as present or absent. It also identifies a negative Trugraf TX Normal designation as immune quiescence; a positive designation was treated as evidence of IA.

The study compares two tacrolimus formulations and dosing schedules in the first year after kidney transplantation. It does not, from the primary endpoint alone, isolate the contribution of either composite component. The clinical question is therefore whether the recorded composite outcome differed between assigned treatment groups over that period, while component-specific secondary outcomes provide additional but separate information.

3. Trial Design

This was a Phase 4, randomized, parallel-group trial with no masking. The registry lists enrollment as 599 and the study status as completed. The recorded study start was 2016-09-09, and primary completion was 2019-06-14. The condition was kidney transplantation, and Astellas Pharma Global Development, Inc. was the sponsor.

One group received once-daily extended-release tacrolimus (Astagraf XL), and the other received immediate-release tacrolimus twice daily. Both regimens began within 48 hours of transplantation at the treating physician’s discretion and were intended for up to 1 year. Dose adjustments were permitted. The immediate-release arm followed an institutionally derived protocol. The registry description of that arm’s dose-adjustment details is truncated, so further specifics are not reported in the registry record.

The primary endpoint timeframe was from the date of transplant until 1 year. The modified Full Analysis Set included randomized participants who received at least 1 dose of either study drug and whose pretransplant cross-matched antibody samples did not demonstrate preformed DSA. The arm counts in the primary outcome analysis were 275 for extended-release tacrolimus and 279 for immediate-release tacrolimus. These are analysis counts, not a restatement of overall enrollment.

Randomization supports a between-group comparison, while the absence of masking means treatment assignment was not concealed from participants or study personnel. How randomization was generated, whether allocation was concealed before assignment, and the trial’s original sample-size justification are not reported in the registry record. The record also does not describe the exact follow-up schedule for the primary composite beyond its overall timeframe.

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: Participants of ≥16 years and ≤70 of age requiring kidney transplant were enrolled. Randomization was stratified by alemtuzumab (yes/no), kidney donor profile index (KDPI) (3 levels: N/A \[living donors\] versus ≤50 versus \>50), and human leukocyte antigens (HLA) Class II mismatch (yes/no).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Modified Full Analysis Set (mFAS) consisted of all participants who were randomized and who received at least 1 dose of study drug (Astagraf XL or BID tacrolimus), and whose pretransplant cross-matched antibody samples did not demonstrate preformed DSA for the duration of the 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: The randomized set consisted of all participants who were randomized to receive the study drug (Astagraf XL or BID tacrolimus).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Were Positive for de Novo DSA (dnDSA) or Immune Activation (IA) Occurrence, measured over From date of transplant until 1 year.

The primary endpoint was the percentage of participants positive for either de novo DSA or IA from transplant until 1 year. It combines an antibody finding with a molecular-assay designation, treating either event as sufficient for a positive composite result. DSA was assessed as a binary variable using a threshold criterion approaching MFI=1000 at any time during the study. IA was classified as present or absent using the Trugraf v2.0 molecular assay. The registry states that a negative Trugraf TX Normal designation represented immune quiescence and that a positive designation was considered evidence of IA in all participants, given the assay’s operating characteristics.

A composite endpoint can capture more than one pathway relevant to the study question and can increase the opportunity to observe an event compared with relying on one component alone. Its interpretation depends on the component definitions: an overall difference would not establish which component drove it, and a similar composite result does not imply that each component had the same frequency. The registry lists component-focused secondary outcomes, including DSA occurrence and IA occurrence, but the primary result is the combined outcome.

The endpoint is a percentage, so the reported group values describe the proportion of analyzed participants meeting at least one criterion. They do not quantify the severity, duration, or clinical consequences of an event. Whether all participants had complete assessment through the full timeframe, and how missing endpoint assessments were handled, are not reported in the registry record.

7. Results Posted in the Registry

• Tacrolimus, Immediate Release BID: 34.4% (96/279) versus 35.6% (98/275) on control; risk difference -1.2 percentage points (95% CI -9.2 to 6.7), risk ratio 0.97 (0.77–1.21); unadjusted two-proportion z-test p = 0.762.

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 DSA Positive Participants With DSA Persistence

• 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:
  • Tacrolimus, Immediate Release BID: 50.0% (6/12) versus 73.3% (11/15) on control; risk difference -23.3 percentage points (95% CI -59.4 to 12.7), risk ratio 0.68 (0.36–1.30); unadjusted two-proportion z-test p = 0.212.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tacrolimus, Immediate Release BID and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of DSA Positive Participants With Human Leukocyte Antigen, Class II, DQ Locus (HLA-DQ)

• 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:
  • Tacrolimus, Immediate Release BID: 25.0% (3/12) versus 40.0% (6/15) on control; risk difference -15.0 percentage points (95% CI -49.9 to 19.9), risk ratio 0.62 (0.20–1.99); unadjusted two-proportion z-test p = 0.411.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tacrolimus, Immediate Release BID and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Were Positive for IA Occurrence From Day 1 to Day 365 Visit

• 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:
  • Tacrolimus, Immediate Release BID: 31.2% (87/279) versus 31.3% (86/275) on control; risk difference -0.1 percentage points (95% CI -7.8 to 7.6), risk ratio 1.00 (0.78–1.28); unadjusted two-proportion z-test p = 0.982.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tacrolimus, Immediate Release BID and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question by separating aspects of DSA and IA, including DSA persistence, HLA-DQ, and IA occurrence. These outcomes can help describe which components may contribute to the composite, but they do not replace the primary comparison. The posted results for IA occurrence are numerically similar between groups, and its recalculated interval spans differences in either direction. The sponsor’s logistic-regression interval for this secondary outcome also includes the no-association value.

Other listed secondary analyses focus on DSA-positive participants. Their smaller analysis groups mean that estimates are less precise and can change substantially with a small number of observations. The record includes a mix of outcomes covering antibody characteristics, persistence, and IA, so results are not all measuring the same phenomenon. Component-level outcomes can illuminate the composite’s makeup, but their interpretation depends on each endpoint’s definition, analysis population, and precision.

The registry lists 60 secondary outcomes and 19 analyses. The overall pattern should not be reduced to a single favorable or unfavorable secondary result: the posted comparisons available in detail do not establish a clear difference, and the restricted analyses are especially uncertain. The registry does not report whether the analyses followed a multiplicity adjustment or a prespecified hierarchy. With many outcomes, unadjusted findings carry less weight because repeated testing can yield apparently notable results by chance. Secondary estimates are best treated as supporting or exploratory context unless a confirmatory analysis plan is documented.

These data do not establish that every secondary endpoint followed the same pattern. The outcome list is broad, while detailed comparison details are available for only a subset. The statistical conclusion should therefore be limited to the outcomes whose results are posted, rather than extended to unreported comparisons or assumed to summarize all secondary measures.

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

• Percentage of Participants Who Were Positive, Negative or Indeterminate for dnDSA Occurrence
• Peak Mean Fluorescence Intensity (MFI) of DSA Positive Participants
• Percentage of DSA Positive Participants With Weak, Moderate and Strong Antibody Strentgh
• Percentage of DSA Positive Participants With DSA Persistence
• Percentage of Participants Who Were Positive or Negative for Complement Component 1, Q Subcomponent (C1q)-Binding DSA
• Percentage of Participants Who Were Positive or Negative for DSA Immunoglobulin G (IgG3) Isotype
• Percentage of DSA Positive Participants With Human Leukocyte Antigen, Class II, DQ Locus (HLA-DQ)
• Percentage of Participants Who Were Positive for IA Occurrence From Day 1 to Day 365 Visit

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the composite definition or did not. The reported percentage is the event proportion within each analysis group. Comparing two such proportions can be expressed as a risk difference, a risk ratio, or an odds ratio. These measures answer related but not identical questions. A risk difference describes an absolute change in event probability; a risk ratio compares event probabilities relative to one another; an odds ratio compares event odds. Odds and probabilities are not interchangeable, so an odds ratio should not be read as a direct percentage-point difference.

What does the unadjusted comparison represent?

The recalculated comparison uses the posted group summaries without adjustment for other variables. It estimates the contrast between the observed event proportions in the two groups. The unadjusted p-value assesses how compatible the observed contrast is with a null hypothesis of no group difference under the calculation’s assumptions. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of a difference.

The recalculated estimate is not the same analysis as the sponsor’s logistic regression. Regression can estimate an odds ratio and may account for covariates if they are included in the model. The registry reports the method as logistic regression but does not report model covariates or other specification details. The recalculated comparison should therefore be understood as a simple, unadjusted check of the posted summaries, not a replacement for a more fully specified trial analysis.

What does the composite endpoint count?

The composite is positive if either de novo DSA or IA is present. The DSA component uses a binary threshold criterion approaching MFI=1000 at any time during the study. The IA component uses the Trugraf v2.0 assay and a present-or-absent designation. Combining components can be useful when the research question concerns more than one related outcome, but it makes the overall result less specific. A change in the composite could arise from one component, both, or a change in which participants meet each component. The composite percentages alone cannot identify that pattern.

How should the model and p-value be read?

Logistic regression models the probability of a binary outcome through its odds. The reported odds ratio is a comparison between groups, but interpreting its direction requires knowing the model’s reference group and coding. The registry lists the groups and an odds ratio of 1.115, but does not give the coding details. The confidence interval describes uncertainty around that model estimate under its analysis assumptions. A p-value summarizes compatibility with a specified null model; it does not show whether an effect is important, or whether a treatment should be chosen.

In general, a confidence interval is a range of values compatible with the data and the method used, at its stated confidence level. An interval containing the no-difference value indicates that the data do not rule out no difference at that level, but it does not establish no effect. An interval can also contain effects in both directions, leaving the direction uncertain. The recalculated interval is reported in the posted comparison, but its confidence level is not stated in the registry entries. The sponsor’s interval is explicitly labelled 95%.

Why does the analysis population matter?

The primary outcome population is not simply everyone enrolled. It is the modified Full Analysis Set: randomized participants who received at least 1 dose of study drug and did not have preformed DSA based on the pretransplant cross-match samples. These conditions define who contributes to the primary outcome analysis and make the result specific to that group. The registry does not describe how many randomized participants were excluded for each reason or how missing outcome measurements were addressed.

Randomization aims to make treatment groups comparable at baseline, on average, but exclusions after randomization and missing observations can affect the interpretation of a particular analysis population. The registry’s description allows the population criteria to be identified; it does not provide enough information to assess the consequences of exclusions or incomplete assessments fully.

Why are secondary analyses more cautious?

The record lists multiple secondary outcomes and analyses. When many outcomes are tested, the chance of at least one apparently notable result can increase, even if there is no underlying difference. A multiplicity adjustment can address some of this issue, but whether a prespecified adjustment or hierarchical testing plan was used is not reported in the registry record. A secondary p-value should therefore be read as an individual analysis result, not automatically as confirmatory evidence.

Some secondary outcomes are assessed only among participants who were DSA-positive. Those analyses concern a selected subgroup and have much smaller group counts than the primary composite analysis. Smaller groups usually produce less precise estimates, especially for binary outcomes. The general statistical point is that fewer observed participants and events tend to leave a wider range of effects compatible with the data; this is not evidence that the subgroup result is inherently more or less important.

The registry reports a total of 61 outcome measures, 60 posted secondary outcomes, and 19 analyses. It does not report a complete statistical analysis plan, model covariates, missing-data procedures, or a multiplicity strategy. Those omissions limit how fully the analysis choices can be evaluated. The posted values can still describe the recorded results, but interpretation should distinguish descriptive contrasts, recalculated unadjusted comparisons, and the sponsor’s reported regression analyses.

11. Confidence Intervals and Precision

For the primary outcome, the unadjusted risk-difference interval extends on both sides of no difference. This means the posted summaries are compatible with a lower composite event proportion in one group as well as a higher proportion; they do not pin down the direction precisely. The unadjusted p-value of 0.762 is consistent with that uncertainty. The interval should not be interpreted as proof of equivalence, because no equivalence margin or non-inferiority criterion is reported.

The sponsor’s logistic-regression estimate is an odds ratio of 1.115, with a 95% confidence interval from 0.760 to 1.636. The interval includes the odds-ratio value corresponding to no association and also extends to values on either side of it. This is an imprecise estimate of the comparative association, rather than a precise demonstration that the groups have the same odds. The registry’s regression model details are not reported, so the interval’s interpretation is conditional on analysis choices that cannot be fully assessed from the record.

Precision depends partly on the amount of information in the analysis. The primary analysis groups contain 275 and 279 participants, while some secondary analyses are restricted to DSA-positive participants and have much smaller group counts. Results from such smaller subgroups can be especially uncertain. Confidence intervals, where available, help show that uncertainty; a percentage alone does not.

A confidence interval is not a range that guarantees the true effect lies within its endpoints. In general, it is a method-based range that reflects sampling uncertainty under assumptions. Its width indicates precision, and its position relative to a no-difference value helps show which directions remain compatible with the data. The registry does not report intervals for every outcome. Where the record gives only percentages, those values should not be mistaken for precise comparative estimates.

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 the primary binary outcome, the figures are participants per arm, rather than total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each illustration uses the stated fraction of the observed effect as the effect to detect. The trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column applies the same idea at a higher probability of detection and therefore requires more participants per arm. For example, using 100% of the observed primary effect gives 23,698 participants per arm for 80% power and 31,724 participants per arm for 90% power. Using 75% of the observed effect gives 42,215 participants per arm for 80% power and 56,513 participants per arm for 90% power.

Smaller effects are harder to distinguish from random variation, so the planning illustrations require more participants when the assumed effect is reduced. This is why the figures rise when planning for 75% or 50% of the observed effect rather than the full observed effect. The curve conveys the same general relationship between effect size and required sample size without changing the underlying assumptions.

These calculations are not observed power. They are prospective planning illustrations derived from the observed contrast, and they should not be used to judge the probability that this completed trial detected a true effect. The sample sizes are especially sensitive to the observed effect: a small observed contrast can produce very large illustrative requirements. Such figures do not by themselves establish whether the original trial was adequately designed, because its original assumptions are not reported.

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 = 0.356; treatment proportion p₁ = 0.344; average p̄ = 0.350.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6746 = 1.3223.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6746 = 0.5677.
4. n = (1.3223 + 0.5677)² / (-0.0123)² = 23,697.3, rounded up to 23,698 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 <- 0.356363636363636                          # control proportion
p1 <- 0.344086021505376                          # 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(2723591)
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 = 23,698 (80% power), 31,724 (90% power)
 75% of observed effect: n per arm = 42,215 (80% power), 56,513 (90% power)
 50% of observed effect: n per arm = 95,172 (80% power), 127,408 (90% power)
power.prop.test: 23697.3 
Simulated power at n = 23,698 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as logistic regression, with an odds ratio of 1.115 and a 95% confidence interval from 0.760 to 1.636. The reported p-value is 0.578 in the record; it is not restated because it exceeds the allowed precision for displayed numbers. The interval includes the no-association value, so the sponsor analysis does not show a clear between-group difference in the primary composite outcome.

The recalculation is a simple, unadjusted comparison of the posted group summaries, expressed as a risk difference. Its interval also spans no difference and effects in either direction, and its unadjusted p-value is 0.762. The two estimates use different statistical measures and methods: logistic regression reports an odds ratio, while the recalculation compares observed proportions without adjustment. They should not be expected to have identical numerical estimates.

The registry does not report the regression model’s covariates, coding details, or other specification choices. Those details would be needed to determine precisely how the adjusted or unadjusted nature of the sponsor estimate compares with the recalculation. The registry record marks no discrepancy between the reported analysis and the recalculated result. Both approaches support a cautious reading: the posted primary data do not establish a clear group difference, and the uncertainty does not demonstrate equivalence.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 61 outcome measures, including 60 secondary outcomes, and 19 analyses. Examining numerous outcomes can increase the chance of finding at least one apparently unusual result by chance. This is the general multiplicity problem: when many statistical tests are performed, isolated p-values can be misleading if their context is ignored. A family-wise adjustment, false-discovery approach, or prespecified testing hierarchy may be used in some studies, but whether any such method was used is not reported in the registry record.

The registry record also does not report a complete statistical analysis plan or explain which outcomes were treated as confirmatory, how analyses were selected, or whether any testing order was prespecified. Without those details, secondary findings should be interpreted cautiously and should not be treated as equally strong evidence merely because they have a reported estimate or p-value. The primary outcome remains the central comparison, with secondary results offering context rather than automatic confirmation.

The primary population is defined as the modified Full Analysis Set: randomized participants who received at least 1 dose of study drug and had no preformed DSA based on pretransplant cross-matched antibody samples. The registry does not report the number excluded for each eligibility criterion, the handling of participants who discontinued treatment, or whether analysis followed assigned group regardless of treatment received beyond this population definition.

Missing outcome data and incomplete follow-up can affect binary event comparisons. The registry does not report the amount or pattern of missing primary endpoint data, any imputation method, or sensitivity analyses addressing missingness. It also does not say how participants without an assessable Trugraf result were classified. Without these details, the extent to which missingness could affect the estimates cannot be assessed. These gaps do not invalidate the posted results, but they limit independent evaluation of the analysis and the robustness of its conclusions.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute kidney injury (10.8%), urinary tract infection (5.6%), hyperkalaemia (5.2%), kidney transplant rejection (4.9%), diarrhoea (3.8%).

The registry reports serious adverse events using separate at-risk counts for each treatment group. In the extended-release group, 163 participants were reported as affected among 288 at risk; in the immediate-release group, 136 were affected among 287 at risk. Deaths were recorded for 2 participants in each group. These are descriptive safety counts, not a randomized efficacy comparison, and no inferential analysis of the between-group safety difference is reported in the registry record.

The listed serious adverse-event terms and percentages include acute kidney injury at 10.8%, urinary tract infection at 5.6%, hyperkalaemia at 5.2%, kidney transplant rejection at 4.9%, diarrhoea at 3.8%, and sepsis at 3.5%. The registry excerpt does not specify whether participants could contribute to more than one event category or give a comparative statistical analysis for these terms. The percentages should therefore be read as reported event frequencies, not as evidence that one regimen caused more or fewer events.

Adverse-event counts can be affected by event definitions, reporting practices, follow-up, and the population used for safety monitoring. These details are not fully reported in the registry record. The safety data describe events recorded during the study; they do not establish causality or provide a complete assessment of the risks of either regimen.

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

The primary result describes the proportion of participants meeting a defined composite endpoint during the first year after transplant. The observed percentages were 35.6% with once-daily extended-release tacrolimus and 34.4% with twice-daily immediate-release tacrolimus. The recalculated comparison and the sponsor’s reported logistic-regression analysis do not establish a clear difference between these groups on that endpoint.

This does not mean the treatments have been shown to be identical. The uncertainty intervals include no difference and effects in either direction, and the registry does not report an equivalence or non-inferiority design. Nor does the result prove that either treatment has no effect on DSA formation or IA. It means that the posted analysis does not resolve a comparative difference with sufficient clarity.

The endpoint is a composite of de novo DSA and IA, so the overall result cannot by itself determine whether the two components behaved similarly. It also does not measure the severity or persistence of each event, graft function, or other outcomes beyond those separately assessed. Secondary results add context but involve multiple outcomes and, for some analyses, much smaller subsets. Their uncertainty and the unreported multiplicity plan limit how strongly isolated findings should be interpreted.

The trial was randomized but unmasked. The primary analysis applies to the registry-defined modified Full Analysis Set, rather than automatically to all people who might receive a kidney transplant. In addition, missing-data procedures and several details of the statistical plan are not reported. Those limitations make the scope of inference narrower than a broad claim about all transplant recipients or all clinically relevant outcomes.

The findings are best understood as an inconclusive comparative result for the registry-defined one-year composite outcome. They do not provide medical advice, a treatment recommendation, or proof of equivalence. Decisions about treatment require clinical context beyond these statistical results.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through its endpoint definition, analysis population, effect measure, and uncertainty—not by comparing percentages alone. The primary outcome combines two biologically distinct signals, antibody formation and molecularly designated immune activation. That design can summarize multiple pathways in one endpoint, while also making it essential to avoid attributing a composite result to one component without component-level evidence.

The example also shows why unadjusted recalculations and sponsor analyses need not have the same numerical estimate. A risk difference compares proportions directly, whereas logistic regression reports an odds ratio. Model details affect interpretation, and the registry does not give enough information to reconstruct all choices in the sponsor analysis. Side-by-side interpretation is useful only when the analysis methods and scales are kept distinct.

Precision is central. The primary estimates do not establish a clear group difference, but neither do they prove that clinically relevant differences are absent. The confidence intervals leave room for more than one direction of effect. Planning illustrations based on the observed contrast can also become very large when that contrast is small, emphasizing how sample-size requirements depend on the effect a future study aims to detect.

Finally, this record highlights the importance of a transparent analysis plan. Multiplicity handling, missing-data procedures, and regression-model details are not reported. Those omissions matter especially when many secondary outcomes are recorded and some analyses are limited to small subsets. A clear registry record can support disciplined interpretation, but the strength of conclusions remains bounded by the methods and details that are documented.

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 leaves several trial-specific uncertainties. It describes randomization and an open-label parallel design but does not report the sequence-generation method or allocation concealment. The treatment descriptions say dose adjustments were allowed, but the immediate-release arm’s detailed dose-adjustment text is truncated. The exact treatment exposure and adherence information are not reported in the registry record.

The primary population excludes randomized participants who did not receive at least 1 dose and those whose pretransplant cross-match samples demonstrated preformed DSA. The numbers excluded under each criterion are not reported. The handling of withdrawals, incomplete endpoint assessments, or missing assay results is also not reported, leaving uncertainty about how these factors may have influenced the analyzed percentages.

The registry identifies logistic regression for the sponsor’s primary analysis but does not report model covariates, coding, or other specification details. It also does not report the original sample-size justification, a complete statistical analysis plan, or a multiplicity strategy. This matters because the record lists numerous outcomes and analyses, including secondary results in relatively small DSA-positive subgroups.

The primary endpoint combines a DSA threshold measure with an IA designation. The composite result cannot identify the contribution of each component, and the registry does not describe all operational details of assessment timing or missing-assay handling. The open-label design is also relevant to outcomes involving study procedures and classification, although the registry does not establish that it introduced bias.

These limitations do not change the posted values, but they constrain assessment of robustness and generalizability. Interpretation should remain focused on the defined analysis population, the recorded one-year composite outcome, and the uncertainty reflected in the reported comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: To Compare the Effects of Immediate-release Tacrolimus and Astagraf XL on Donor-Specific Antibody (DSA) Formation and the Development of Immune Activation (IA) in de Novo Kidney Transplant Recipients — NCT02723591.
• Registry record last updated 2024-12-18; status last verified 2024-11.
• Results first posted 2020-06-29.
• 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

NCT02723591 was a completed Phase 4 randomized, open-label, parallel-group trial sponsored by Astellas Pharma Global Development, Inc. It compared once-daily extended-release tacrolimus (Astagraf XL) with twice-daily immediate-release tacrolimus in de novo kidney transplant recipients. The study began on 2016-09-09, and primary completion was recorded on 2019-06-14.

The primary outcome was the percentage positive for de novo DSA or IA from transplant until 1 year, among the modified Full Analysis Set. The posted percentages were 35.6% and 34.4%, respectively. Both the recalculated unadjusted comparison and the sponsor’s logistic-regression result are inconclusive for a between-group difference. The registry lists multiple secondary outcomes and safety events, while key details about missing data, multiplicity, and statistical model specification are not reported in the registry record.