Study to Assess the Efficacy and Safety of Bleselumab in Preventing the Recurrence of Focal Segmental Glomerulosclerosis in de Novo Kidney Transplant Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Efficacy and Safety of Bleselumab in Preventing the Recurrence of Focal Segmental Glomerulosclerosis in de Novo Kidney Transplant Recipients (NCT02921789), a randomized phase 2 study. The primary outcome is Percentage of Participants With Recurrence of Focal Segmental Glomerulosclerosis (rFSGS) or Death or Graft Loss or Lost to Follow-up Through 3 Months Post Transplant.

2. Clinical Question

3. Trial Design

This was a Phase 2a, randomized, open-label, active-control, multicenter study of bleselumab in de novo kidney transplant recipients with primary FSGS. Its stated purpose was to assess efficacy and safety in preventing recurrent FSGS. The record describes a parallel-group design: participants were assigned to the bleselumab regimen or the standard-of-care regimen, rather than crossing between treatments. Masking was listed as none, so the study was open-label.

The bleselumab regimen included basiliximab induction, bleselumab, tacrolimus, and steroids. The standard-of-care regimen included basiliximab induction, MMF, tacrolimus, and steroids. Thus, the comparison concerned two treatment regimens that shared several components and differed in the listed maintenance agent. The record describes the regimens but does not report a rationale for choosing the allocation procedure or an account of how randomization was implemented.

Registry enrollment was 67. The primary outcome results use analysis groups of 32 in the standard-of-care arm and 27 in the bleselumab arm. Those analysis counts should not be conflated with the enrollment figure: the primary analysis population had specific eligibility conditions, and the record states that participants later confirmed to have secondary FSGS were excluded from the Full Analysis Set. The complete flow from enrollment through each analysis group, including reasons for any differences, is not reported in the registry record.

The study began on 2017-05-22, reached primary completion on 2020-12-11, and is listed as completed. The primary outcome was assessed through 3 months post-transplant. Secondary outcomes included longer follow-up for recurrence or certain events, biopsy-proven acute rejection, efficacy failure, and biopsy-proven recurrence. The registry record does not report the trial’s original sample-size justification, its detailed statistical analysis plan, or whether interim analyses were planned or conducted.

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: Male or female participants with ≥ 18 years of age who were recipient of a de novo kidney from a living or deceased donor and has biopsy proven, primary focal segmental glomerulosclerosis (pFSGS) as a cause of ESRD in their native kidneys and their most current graft failure(s) was due to biopsy-proven, recurrent focal segmental glomerulosclerosis (rFSGS).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consisted of all participants who are randomized, receive at least one dose of study drug and receive a transplanted kidney. Participants who were later confirmed to have secondary FSGS were excluded from the FAS population because they were not at risk for recurrence post-transplant. Participants with available data at specified time point were included.

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: Safety (SAF) population: All participants who were randomized and received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Recurrence of Focal Segmental Glomerulosclerosis (rFSGS) or Death or Graft Loss or Lost to Follow-up Through 3 Months Post Transplant, measured over At 3 Months post transplant.

The primary endpoint is the percentage of participants with recurrent FSGS, death, graft loss, or loss to follow-up through 3 months after transplantation. Recurrent FSGS was defined by nephrotic-range proteinuria with a protein-creatinine ratio of at least 3.0 g/g. The endpoint combines a disease recurrence definition with events that can prevent recurrence from being observed or evaluated. Under the stated definition, death, graft loss, and loss to follow-up were imputed as recurrence rather than treated as uncomplicated missing observations.

A binary percentage endpoint gives the proportion of the analyzed group classified as having the outcome. It is useful for communicating how frequently an event or composite occurred during a specified period. Here, the composite includes clinically different circumstances: measured proteinuria meeting the recurrence threshold, death, graft loss, or loss to follow-up. As a result, the percentage represents the endpoint as defined, not a count of biopsy-confirmed recurrence alone.

For the primary outcome, the registry reports 31.3% in the standard-of-care group and 18.5% in the bleselumab group. The corresponding 95% confidence intervals are 16.1% to 50.0% and 6.3% to 38.1%. These intervals express uncertainty around each group’s estimated percentage. The endpoint and its follow-up period are important to interpretation: the results concern this composite through 3 months, not recurrence at every later time or every possible definition of FSGS recurrence.

7. Results Posted in the Registry

• Bleselumab Regimen: 18.5% (5/27) versus 31.2% (10/32) on control; risk difference -12.7 percentage points (95% CI -34.5 to 9.0), risk ratio 0.59 (0.23–1.52); unadjusted two-proportion z-test p = 0.263.

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 Efficacy Failure Through 12 Months Post Transplant

• 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:
  • Bleselumab Regimen: 33.3% (9/27) versus 31.2% (10/32) on control; risk difference 2.1 percentage points (95% CI -21.9 to 26.0), risk ratio 1.07 (0.51–2.24); unadjusted two-proportion z-test p = 0.865.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bleselumab Regimen and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes involving recurrence or death, graft loss, or loss to follow-up through 6 and 12 months; biopsy-proven acute rejection through 3, 6, and 12 months; efficacy failure through 12 months; and biopsy-proven recurrence through 3, 6, and 12 months. Numerical results are available in the registry record for efficacy failure through 12 months, but results for the other listed secondary outcomes are not reported in the registry record in the information available for this analysis.

For the posted efficacy-failure outcome, the percentages were 32.3% for standard of care and 32.0% for bleselumab. The recalculated risk difference is 0.021, with a 95% confidence interval from -0.219 to 0.260. The sponsor reports a difference of -0.3, a 95% confidence interval from -24.9 to 24.3, and p = 1.0. These estimates are imprecise and do not establish a difference between regimens. Their interpretation is limited to this secondary endpoint and its 12-month timeframe.

The primary outcome and the efficacy-failure result address related but distinct questions. The primary endpoint is a composite through 3 months with a specified recurrence definition and imputation rule. The secondary endpoint has a different title and follow-up period; its full operational definition is not reported in the registry record. A similar-looking percentage should not be treated as a replication of the primary endpoint or as a direct test of the same outcome over a longer period.

Secondary analyses usually carry less inferential weight than the primary analysis because they may be numerous, may not be the main basis for the study’s conclusion, and can be vulnerable to multiplicity. When many outcomes or timepoints are examined, the chance of apparently notable results arising by chance can increase. The registry record does not report a multiplicity adjustment or a detailed hierarchy for interpreting secondary results. The safest reading is descriptive: consider the reported estimates and their uncertainty, avoid treating isolated secondary p-values as confirmatory, and do not infer an overall pattern from outcomes whose numerical results are not reported.

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

• Percentage of Participants With rFSGS or Death or Graft Loss or Lost to Follow-up Through 6 and 12 Months Post Transplant
• Percentage of Participants With Biopsy-Proven Acute Rejection (BPAR) Through 3, 6, and 12 Months Post Transplant
• Percentage of Participants With Efficacy Failure Through 12 Months Post Transplant
• Percentage of Participants With Biopsy Proven rFSGS Through 3, 6 and 12 Months Post-Transplant

9. Statistical Interpretation

10. Statistical Methods Explained

Binary-outcome methods describe whether participants did or did not meet an outcome definition during a stated period. For this trial, the primary endpoint is expressed as a percentage of participants with the composite outcome through 3 months post-transplant. The percentage is an estimate of the event frequency in the analyzed group, not a measure of the severity of an event or the time at which it occurred.

What does a risk difference describe?

A risk difference compares two event percentages by subtracting one group’s event proportion from the other’s. Its sign depends on the order of the groups in the contrast. In the posted recalculation, the comparison is bleselumab against standard of care, and the estimate is -0.127. This direction indicates a lower observed event proportion in the bleselumab group. The risk difference is an absolute contrast, unlike a risk ratio or odds ratio, which expresses a relative comparison.

The reported recalculated risk ratio is 0.593, with a 95% confidence interval from 0.231 to 1.522. The odds ratio is 0.5, with a 95% confidence interval from 0.147 to 1.703. These relative measures are based on the same binary outcome but answer different questions from the risk difference. Their intervals include the null value for their respective measures, just as the risk-difference interval includes zero. Relative measures can be less intuitive when event percentages are not rare, and odds ratios should not be read as if they were risk ratios.

Why use confidence intervals?

A confidence interval gives a range of effect estimates compatible with the observed data under the method’s assumptions. A 95% confidence interval is a procedure with a repeated-sampling interpretation: if the same method were applied across repeated comparable studies, intervals would contain the underlying parameter at the stated rate. It is not a probability statement that the specific parameter lies in the particular interval. For this trial, the interval around the risk difference extends from -0.345 to 0.090, so it allows a range of possible effects, including no difference. Its width is a key part of interpretation, not a detail to set aside in favor of the point estimate.

Why can analyses give different p-values?

The sponsor reports a Fisher Exact analysis for the primary difference, with p = 0.370. The simple recalculation gives p = 0.263. Different analysis procedures can yield different p-values because they may use different assumptions, reference distributions, or ways of handling the discrete outcomes. A Fisher Exact test uses the observed allocation of binary outcomes to evaluate the comparison under its null hypothesis. The recalculation is an unadjusted computation from posted summary information, not a replacement for the sponsor’s prespecified analysis. The registry record does not report enough detail to attribute every difference between the inferential results to a particular implementation choice. The sponsor’s own analysis takes precedence as the trial-reported analysis.

Small event counts can make binary comparisons imprecise. In general, when the number of observed outcomes is limited, estimates can change noticeably with a small change in the observed data, and confidence intervals may remain broad. This is one reason to consider estimates and intervals together rather than relying only on a p-value. It is also a reason not to treat the absence of a statistically persuasive difference as proof of equal effects.

What does over-dispersion mean?

Over-dispersion is a general concept for data that vary more than a statistical model expects. It is especially relevant to count outcomes when a simple model assumes that observations vary according to a particular distribution. The primary endpoint is a binary percentage, and the registry record does not identify an over-dispersion adjustment for this comparison. It would be inappropriate to infer that such an adjustment was used or needed. More generally, methods should reflect the outcome type and the structure of the data; conclusions can be sensitive when model assumptions do not fit the data well.

How should the analysis population be understood?

The Full Analysis Set is described as participants who were randomized, received at least one dose of study drug, and received a transplanted kidney, with later-confirmed secondary FSGS excluded because those participants were not considered at risk for recurrence. This definition is not identical to simply counting everyone enrolled. The primary arm counts are 32 and 27. The registry record does not give a complete participant flow or all exclusions by reason, so the available results should be interpreted for the stated analysis population rather than assumed to represent every enrolled participant.

For the primary composite, death, graft loss, and loss to follow-up were imputed as recurrence. Imputation is a rule for assigning an outcome when the event cannot be observed in the usual way; it does not mean that each such participant had documented proteinuria meeting the recurrence definition. The rule makes the composite conservative in one sense, by classifying these outcomes as failures, but it also changes what the endpoint represents. The registry record does not report other details of missing-data handling or sensitivity analyses.

Finally, the record reports multiple outcomes, including secondary outcomes and safety measures. Examining many outcomes can increase the chance of observing apparently notable results by chance, particularly when analyses are not adjusted for multiple comparisons. The multiplicity procedure, if any, is not reported in the registry record. Accordingly, individual secondary comparisons should be treated as exploratory unless the trial’s full analysis plan establishes otherwise.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. The primary group percentages have 95% confidence intervals of 16.1% to 50.0% for standard of care and 6.3% to 38.1% for bleselumab. Each interval covers a broad range of event percentages, indicating that the observed group estimates are not highly precise. The comparison interval is likewise broad: the recalculated risk difference is -0.127, with a 95% confidence interval from -0.345 to 0.090.

That comparison interval includes zero, the value corresponding to no absolute difference. It also includes values on either side of zero, so the observed data do not sharply distinguish a lower event percentage with bleselumab from no difference or a higher percentage. The point estimate is one plausible value, but the interval makes clear that substantially different effects remain compatible with the data under the calculation’s assumptions.

Confidence intervals are not guarantees that the true effect lies within their limits, nor are they a direct measure of clinical importance. They quantify sampling uncertainty under a specified method. The registry’s group intervals describe uncertainty in each percentage; they should not be used as a substitute for the interval on the between-group contrast. The comparison interval directly addresses the difference between regimens.

The sponsor’s interval for the primary difference is -34.5 to 9.0, with a reported difference of -12.7. It too includes zero and is wide. The sponsor’s and recalculated results use different reported forms and analysis procedures, so their intervals should be read in the context of their respective methods. Both portray meaningful uncertainty rather than a precise estimate. The available group sizes and outcome counts help explain why the results are not tightly estimated, but the registry record does not report a precision target or the original sample-size rationale.

For the secondary efficacy-failure comparison, the group intervals are also broad, and its recalculated difference interval crosses zero. This further illustrates that the posted comparisons are not precise enough to support strong claims from point estimates alone. Precision is improved by accumulating informative outcome data, but the registry record does not establish what size or duration would be adequate for a definitive estimate.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For these binary outcomes, the entries are participants per arm, not total participants and not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities under assumptions, not probabilities that a particular result is correct. This is not observed power: it does not measure the probability that the completed trial has demonstrated an effect.

The planning scenarios are anchored to the observed effect and then consider detecting 100%, 75%, or 50% of that effect. As the target effect becomes smaller, more participants are required to distinguish it from random variation at the stated power and significance level. The large figures associated with some smaller-effect scenarios reflect how difficult it can be to detect a modest difference in a binary outcome when the event percentages are similar. They do not mean that the trial enrolled that many participants or that the registry planned to enroll those numbers.

The calculations are sensitive to their assumptions. Equal allocation, a normal approximation, and the chosen effect size are features of the illustration, not reported features of the original trial design. A planning curve can help readers see how the required sample size changes as the target effect changes, but it cannot compensate for uncertainty about the true effect or differences between the planning assumptions and an eventual study. The figures should therefore be read as conditional planning examples, not as evidence about the quality of the completed study or the probability that its result is true.

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 = 0.312; treatment proportion p₁ = 0.185; average p̄ = 0.249.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6114 = 1.1984.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6048 = 0.5090.
4. n = (1.1984 + 0.5090)² / (-0.1273)² = 179.8, rounded up to 180 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 <- 0.3125                          # control proportion
p1 <- 0.185185185185185                          # 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(2921789)
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 = 180 (80% power), 241 (90% power)
 75% of observed effect: n per arm = 334 (80% power), 447 (90% power)
 50% of observed effect: n per arm = 781 (80% power), 1,045 (90% power)
power.prop.test: 179.8 
Simulated power at n = 180 per arm: 0.807 (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’s reported primary comparison uses Fisher Exact and gives a difference of -12.7, a 95% confidence interval from -34.5 to 9.0, and p = 0.370. The simple unadjusted recalculation gives a risk difference of -0.127, with a 95% confidence interval from -0.345 to 0.090 and p = 0.263. The numerical estimates express the same direction: the observed primary percentage was lower in the bleselumab group. The inferential results are not identical.

Different procedures can produce different p-values and confidence intervals, particularly with binary outcomes and limited event counts. The registry record does not report enough detail to identify every reason for the difference. The discrepancy indicator is false, but the recalculated result remains a simple, unadjusted calculation from posted summary statistics rather than the trial’s own analysis. The sponsor’s own analysis takes precedence when reporting what the study’s analysis found.

Neither analysis gives a confidence interval that excludes zero, and neither supports a definitive claim about the direction or size of the underlying effect. The sponsor’s p-value should not be interpreted as the probability that there is no effect, and the recalculated p-value should not be substituted for the sponsor’s result. Read together, the results indicate a lower observed percentage in the bleselumab group but substantial uncertainty about the comparative effect.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and several secondary outcomes, including assessments at different follow-up times. When a study tests multiple outcomes, timepoints, or comparisons, the probability of at least one apparently unusual result by chance can increase. Multiplicity procedures can control that risk, for example by adjusting the threshold for interpretation or by specifying an ordered testing strategy. The registry record does not report whether such a procedure was planned or used, and no detailed statistical analysis plan is reported. The primary analysis should therefore be distinguished from the additional secondary comparisons, which should not automatically be treated as confirmatory.

The primary population is described as the Full Analysis Set. It includes participants who were randomized, received at least one dose of study drug, and received a transplanted kidney. Participants later confirmed to have secondary FSGS were excluded because they were not considered at risk for recurrence. This definition informs which participants contribute to the reported primary endpoint. The registry record does not provide a complete accounting of all participants by analysis population or a full flow explaining the difference between enrollment and the primary analysis groups.

The primary outcome rule classifies death, graft loss, or loss to follow-up as recurrence. This is an explicit imputation rule for those events in the composite. It should not be mistaken for direct observation of recurrent FSGS in every participant counted as having the outcome. Other missing-data procedures, the handling of any unavailable measurements, and sensitivity analyses are not reported in the registry record.

These omissions limit assessment of robustness. A sensitivity analysis could examine whether conclusions change under alternative assumptions about missing outcomes or analysis populations, but no such results are reported. Likewise, the record does not describe interim analyses, stopping rules, or a sample-size justification. These details cannot be inferred from the observed enrollment or the posted outcome results. Their absence from the registry record does not establish that a procedure was or was not used; it means that the reported information is insufficient to evaluate it.

Because the trial is open-label, participant and investigator knowledge of assigned regimen may also affect aspects of care or outcome assessment. The objective proteinuria threshold provides a defined criterion, but the composite includes events and follow-up status that can involve judgment or ascertainment. The record does not report specific safeguards for outcome assessment. This is a consideration when weighing the analysis, not evidence that the results were biased.

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: kidney transplant rejection (14.7%), focal segmental glomerulosclerosis (10.3%), acute kidney injury (8.8%), hydronephrosis (8.8%), dehydration (6.9%).

The serious adverse-event figures use safety groups of 34 participants at risk in the standard-of-care regimen and 29 in the bleselumab regimen. Serious adverse events affected 16 participants in each group. Other adverse events affected 29 of 34 participants in the standard-of-care group and 28 of 29 in the bleselumab group. The registry reports zero deaths in both safety groups. These counts describe participants affected, not the total number of events; one participant may have experienced more than one event.

The registry’s leading serious adverse-event terms include kidney transplant rejection at 14.7%, focal segmental glomerulosclerosis at 10.3%, acute kidney injury at 8.8%, hydronephrosis at 8.8%, dehydration at 6.9%, and cytomegalovirus infection at 5.9%. These terms describe events recorded in the study and should not be read as proof that a regimen caused them. The registry record does not provide enough detail to compare event severity, duration, relatedness assessments, or timing by regimen.

Safety counts are descriptive and use different denominators from the primary efficacy analysis. They should not be combined with efficacy percentages or interpreted as a randomized comparison without considering the event definitions and available follow-up. The absence of reported deaths in these groups does not establish the absence of other serious risks, and the figures alone cannot characterize the full safety profile.

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

The primary result describes the percentage of participants who met a specified composite outcome through 3 months after kidney transplantation. The observed percentage was 31.3% with standard of care and 18.5% with the bleselumab regimen. The comparison’s reported and recalculated estimates point toward a lower observed percentage with bleselumab, but the uncertainty intervals include no difference and are broad. The results therefore do not establish a reliable reduction in the primary composite, nor do they rule out effects in either direction.

The conclusion applies to the trial’s analysis population, outcome definition, and follow-up period. It does not isolate proteinuria-defined recurrence from death, graft loss, or loss to follow-up, because those latter events were counted as recurrence. It also does not answer whether the regimens differ for biopsy-proven recurrence, for outcomes beyond the specified period, or for every secondary outcome. Numerical results for several listed secondary outcomes are not reported in the registry record.

A lack of a clear statistical difference is not proof that the regimens are equivalent. Equivalence requires a prespecified margin and an analysis designed to test whether the effect lies within that margin; such a margin is not reported. Nor does a lower point estimate by itself demonstrate a clinically important benefit. Clinical importance depends on the size and reliability of the effect, the outcome’s meaning, and the balance of potential benefits and harms. The registry information does not establish that balance.

The study’s open-label design, limited analysis-group sizes, broad intervals, composite outcome, and incomplete reporting of analysis details constrain interpretation. The results are best understood as estimates from a randomized comparison with substantial uncertainty, rather than as a definitive answer about the comparative efficacy or safety of the regimens. They do not justify medical advice for an individual transplant recipient.

18. Why This Trial Matters Statistically

This trial addresses a defined question in a population for whom recurrence of primary FSGS after kidney transplantation is an important study outcome. Statistically, it illustrates the difference between an observed contrast and a precise estimate of a treatment effect. The lower primary percentage in the bleselumab group is the point estimate; the wide confidence interval shows that the available data leave substantial uncertainty around that contrast.

The example also shows why analysis details matter. The sponsor reports a Fisher Exact comparison, while a simple unadjusted recalculation yields a different p-value. Both analyses point in the same direction for the estimate, but neither interval excludes no difference. Presenting the sponsor’s own analysis alongside a clearly identified recalculation helps readers distinguish the trial’s reported inference from a secondary check based on summary statistics.

The composite endpoint raises a further statistical question: what exactly does the event percentage represent? It includes proteinuria-defined recurrence as well as death, graft loss, and loss to follow-up classified as recurrence. This rule may help prevent unavailable recurrence status from being treated as a favorable outcome, but it also means the endpoint is broader than documented recurrence alone. Clear outcome definitions are essential for interpreting percentages and comparing studies.

Finally, the record illustrates the limits of secondary-outcome interpretation when many outcomes and timepoints are listed but multiplicity procedures and full results are not reported. The primary result can be described, but missing analytical detail limits assessment of how confirmatory the additional findings are. These are general lessons in reading clinical-trial evidence: inspect the endpoint, analysis population, effect estimate, uncertainty, and reporting completeness together.

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 primary comparison is based on analysis groups of 32 and 27, and the confidence intervals are broad. This limits precision and makes the result sensitive to the small number of observed outcomes. Registry enrollment was 67, but the record does not provide a full participant-flow account that explains all differences between enrollment and the primary analysis groups.

The primary outcome is a composite. Its definition includes recurrence based on a protein-creatinine threshold, while death, graft loss, and loss to follow-up are imputed as recurrence. The posted percentage therefore cannot be interpreted as the percentage with documented recurrent FSGS alone. The record does not provide component-specific primary results in the information available for this analysis.

The trial was open-label, with no masking. The proteinuria criterion is specified, but open-label conduct can matter for care, follow-up, and outcome ascertainment. The registry record does not describe specific procedures used to limit potential assessment bias. This concern should be acknowledged without assuming that bias occurred.

The sponsor’s Fisher Exact result and the simple unadjusted recalculation differ numerically. The sponsor’s analysis takes precedence, but the registry information does not include a full statistical analysis plan to explain every implementation detail. The original sample-size justification, interim-analysis procedures, multiplicity strategy, and detailed missing-data sensitivity analyses are not reported in the registry record.

Only one secondary outcome has numerical results in the information available for this analysis. The other listed secondary outcomes cannot be used to establish a broader pattern because their results are not reported in the registry record. Safety counts are descriptive, use safety denominators that differ from the primary analysis groups, and do not by themselves establish causation or fully characterize comparative safety. These limitations constrain how broadly the findings can be interpreted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess the Efficacy and Safety of Bleselumab in Preventing the Recurrence of Focal Segmental Glomerulosclerosis in de Novo Kidney Transplant Recipients — NCT02921789.
• Registry record last updated 2024-12-04; status last verified 2024-11.
• Results first posted 2022-01-05.
• 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

NCT02921789 is a completed Phase 2a, randomized, open-label, active-control, parallel-group, multicenter study of bleselumab in de novo kidney transplant recipients with primary FSGS. Registry enrollment was 67. The primary outcome was the percentage with recurrent FSGS, death, graft loss, or loss to follow-up through 3 months after transplant, with the latter events imputed as recurrence.

The posted primary percentages were 31.3% for standard of care and 18.5% for bleselumab. The sponsor reported a Fisher Exact difference of -12.7, with a 95% confidence interval from -34.5 to 9.0 and p = 0.370. The recalculated risk-difference interval also includes zero. The estimates are uncertain and do not establish a definitive comparative effect.

The record lists secondary efficacy and safety outcomes, but numerical results for several listed secondary outcomes are not reported in the registry record. The original sample-size justification, detailed analysis plan, multiplicity procedures, and additional missing-data analyses are also not reported.