Focal Segmental Glomerulosclerosis Clinical Trial (FSGS-CT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Focal Segmental Glomerulosclerosis Clinical Trial (FSGS-CT) (NCT00135811), a randomized phase 3 study. The primary outcome is Partial or Complete Proteinuria Remission at 52 Weeks (Score 1-3).

2. Clinical Question

The study was a prospective, controlled, randomized, multicenter, open-label trial. The primary outcome’s remission definition was based on urine protein/creatinine (Up/c), with score categories also reflecting remission status at specified time points. The registry describes complete remission as Up/c <0.2 and partial or complete remission as Up/c <2.0. The posted outcome count is the number of participants meeting the score 1–3 definition in each arm.

This question is about a comparison between two treatment strategies, not about either strategy in isolation. Random allocation is intended to make treatment groups comparable on average, while the open-label design means masking was not used. The registry record does not report additional details about eligibility, treatment administration, or the rules used to assign participants to the outcome categories.

3. Trial Design

The Focal Segmental Glomerulosclerosis Clinical Trial (FSGS-CT), registry identifier NCT00135811, is listed as a phase 3, randomized, parallel-group trial with no masking. Its registry status is completed. The sponsor is the National Institute of Diabetes and Digestive and Kidney Diseases (NIDDK).

The registry describes the study as multicenter, prospective, controlled, and open label. Participants were assigned to cyclosporin or MMF/DEX. The trial summary frames the intended comparison as MMF with pulse steroids versus Cyclosporine-A for inducing proteinuria remission over 12 months. The registry reports enrollment of 192. The reported primary-outcome counts have denominators of 72 in the cyclosporin arm and 66 in the MMF/DEX arm; these denominators describe the posted outcome data and should not be assumed to explain the full enrollment figure.

The study start is recorded as 2004-11, and primary completion as 2009-11. The primary outcome is partial or complete proteinuria remission at 52 weeks, based on scores from 1 to 3. A secondary outcome is remission at 78 weeks. Both outcomes are presented as participant counts.

Open-label means that masking was not used, according to the registry. In general, lack of masking can matter when treatment knowledge could affect care, outcome assessment, or participant behavior. The posted endpoint uses defined urine protein/creatinine thresholds and score categories, but the registry record does not report whether outcome assessors were masked or how the outcome was adjudicated.

Details such as the intended allocation ratio, the original sample-size justification, the trial’s own statistical analysis plan, planned interim analyses, and analysis-population definitions are not reported in the registry record. The planning illustrations associated with the posted results are not the trial’s original design assumptions.

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: Of 192 enrolled participants, 54 were excluded before randomization because they were ineligible. The most common reasons for exclusion were lack of an FSGS lesion on kidney biopsy (n=18), urine protein/creatinine ratio \<1 (n=20), and estimated glomerular filtration rate \<40 mL/min/1.73 m² (n=5). A total of 138 participants were randomized.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Partial or Complete Proteinuria Remission at 52 Weeks (Score 1-3), measured over 52 weeks.

The primary endpoint is the number of participants with partial or complete proteinuria remission at 52 weeks, defined by a score from 1 to 3. The registry describes proteinuria scores as ranging from 1, most favorable, to 6, least favorable. The primary analysis is described as the percent of patients with scores of 1–3.

Partial or complete remission is defined as urine protein/creatinine (Up/c) <2.0, while complete remission is defined as Up/c <0.2. The score categories combine measurements across time. Score 6 represents failure to achieve partial or complete remission during weeks 2–26. Score 5 represents achieving remission at least once between weeks 2 and 20 but not at week 26. Score 4 represents remission at week 26 but not week 52. Score 3 represents remission at both week 26 and week 52. Score 2 adds an Up/c value of at least 0.2 at least once during weeks 26–52, while score 1 requires Up/c <0.2 for all measurements during weeks 26–52.

Using a defined remission endpoint makes the treatment comparison interpretable in terms of participants meeting a specified clinical and laboratory-based outcome. Collapsing scores 1–3 into the primary outcome creates a binary comparison: meeting the remission definition or not meeting it. The registry does not report further details about missing measurements or how incomplete score histories were handled.

7. Results Posted in the Registry

• MMF/DEX: 33.3% (22/66) versus 45.8% (33/72) on control; risk difference -12.5 percentage points (95% CI -28.7 to 3.7), risk ratio 0.73 (0.48–1.11); unadjusted two-proportion z-test p = 0.134.

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.

Partial or Complete Proteinuria Remission at 78 Weeks (Score 1-3)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • MMF/DEX: 25.8% (17/66) versus 22.2% (16/72) on control; risk difference 3.5 percentage points (95% CI -10.7 to 17.8), risk ratio 1.16 (0.64–2.10); unadjusted two-proportion z-test p = 0.627.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MMF/DEX and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: partial or complete proteinuria remission at 78 weeks. Its overall pattern does not reinforce a clear, precise difference between the arms. The direction of the unadjusted point estimate differs from the primary comparison, while the interval remains compatible with no difference and with effects in either direction. This makes the later result a useful additional description of remission, but not a decisive resolution of the uncertainty in the primary result.

Secondary outcomes can help assess whether findings are consistent across outcome times or definitions. In this trial, the primary endpoint is remission at 52 weeks, and the listed secondary endpoint is remission at 78 weeks. The latter is related to the primary question, but it is not a substitute for the primary analysis and does not erase the uncertainty around it.

Unadjusted secondary results generally carry less evidential weight than a prespecified primary comparison. When multiple outcomes or comparisons are examined, the chance of observing an apparently notable result by chance can increase. In general, multiplicity procedures or a prespecified hierarchy can address that issue, but the registry record does not report a multiplicity plan for this trial. The posted secondary result should therefore be read as supportive descriptive information, not as an independent confirmatory finding.

The registry identifies two outcome measures and two analyses overall, but the original analysis plan and the full set of planned comparisons are not reported. It is consequently not possible to determine from the registry record whether the listed secondary endpoint was selected in advance, whether additional outcomes were analyzed but not posted, or how the investigators intended to interpret multiple results together.

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

• Partial or Complete Proteinuria Remission at 78 Weeks (Score 1-3)

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute? In general, random assignment is used to reduce systematic differences between treatment groups at the start of a trial. It does not guarantee that groups will be identical, particularly in a finite study, and it does not remove uncertainty from the outcome comparison. The registry identifies this study as randomized but does not report the allocation procedure, concealment details, or the intended allocation ratio.

What is the outcome scale? The primary endpoint is binary for the posted comparison: each participant either has a score from 1 to 3 or does not. The underlying score contains ordered categories, from 1, most favorable, to 6, least favorable, but the registry’s primary analysis groups scores 1–3 together. The posted arm values are counts of participants meeting that definition. A risk difference describes the absolute difference between the proportions in the two arms. A negative risk difference for MMF/DEX relative to cyclosporin means that the observed proportion is lower in the MMF/DEX arm.

How should an odds ratio be understood? In general, an odds ratio compares the odds of an outcome between groups. An odds ratio of 1 is the no-difference reference value; estimates below 1 indicate lower odds in the group named relative to its comparator. Odds ratios and risk differences are different scales and need not have the same numerical size. The registry posts the sponsor’s estimate as an odds ratio but does not report the method used to obtain it. The recalculated odds ratio is a simple unadjusted calculation from the posted summary counts.

What does a p-value describe? In general, a p-value measures how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The unadjusted p-values associated with the simple recalculations are not substitutes for an analysis that may account for design features or other prespecified considerations. The registry record does not report the sponsor analysis method or a sponsor p-value.

What is a confidence interval? In general, a confidence interval is a range of estimates compatible with the observed data under a particular statistical procedure. Its width conveys precision: wider intervals allow a broader range of underlying effects. Whether the interval includes the no-difference value helps describe uncertainty, but an interval should not be read as a list of effects known to be true. The intervals in the posted results are based on the corresponding estimates and methods; the sponsor method is not reported in the registry record.

Why distinguish reported and recalculated analyses? The sponsor analysis is the analysis posted by the registry as a reported result. The recalculated comparisons are simple unadjusted calculations using the displayed arm counts. They are useful for reading the raw contrast consistently across outcomes, but they may not reproduce an analysis that uses additional covariates, stratification, or other design information. Such details are not reported in the registry record. The discrepancy indicator is false, so no discrepancy is flagged between the sponsor result and recalculation.

What does open-label mean statistically? The registry lists masking as none. In general, treatment awareness can influence behaviors, concomitant care, reporting, or assessment, depending on the outcome and study conduct. The remission endpoint is based on urine protein/creatinine thresholds and a score defined across visits, which gives it explicit measurement rules. However, the registry record does not say whether assessments were conducted by people unaware of treatment assignment, nor does it describe procedures to limit measurement bias.

What can be inferred from the counts? The counts directly describe the number of participants classified as having the outcome in each arm among the denominators posted for that analysis. They do not by themselves establish that every enrolled participant contributed an endpoint. They also do not describe the reasons for missing outcomes or whether the analysis followed an intention-to-treat principle. Those analysis-population and missing-data details are not reported in the registry record.

For binary outcomes, over-dispersion is generally not the central issue in the way it can be for count models; the main concerns include outcome definition, group denominators, missingness, and the chosen comparison method. In general, over-dispersion means that observed variability is greater than a model assumes, which can make standard errors too small if not handled appropriately. The registry does not report an over-dispersion assessment, and the posted endpoint is presented as participant counts rather than a rate or recurrent-event count.

The statistical methods that governed the original trial, including its prespecified primary comparison, multiplicity approach, interim analyses, missing-data procedures, and sample-size justification, are not reported in the registry record. The calculations and descriptions associated with the posted summary statistics should therefore be distinguished from the original protocol’s planned analyses.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.125, with a 95% confidence interval from -0.287 to 0.037. The interval spans zero, so the observed data are compatible with no difference and with differences in either direction. Its width also means that the estimate does not pin down the size of the underlying contrast precisely. The point estimate alone should not be treated as a settled estimate of the treatment contrast.

The sponsor’s odds-ratio estimate is 0.59, with a 95% confidence interval from 0.3 to 1.18. The interval includes 1, the null value for an odds ratio. The registry does not report a p-value for this sponsor analysis, and it does not describe the method used to construct the interval. The unadjusted recalculated odds ratio is 0.591, with a confidence interval from 0.296 to 1.179. Those recalculated values are not a replacement for the sponsor analysis.

For the 78-week comparison, the recalculated risk difference is 0.035, with a 95% confidence interval from -0.107 to 0.178. This interval also includes zero. In general, overlapping possibilities around the no-difference value indicate uncertainty about the direction and size of a group contrast, not proof that the groups are identical.

Confidence intervals describe statistical uncertainty under the method used; they do not account automatically for possible bias, incomplete outcome data, or limitations in how the analysis was reported. The registry record does not report the sponsor’s statistical method or the handling of missing observations, so those sources of uncertainty cannot be evaluated from the posted information alone.

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 illustrations are expressed as participants per arm because these outcomes are binary participant counts, not time-to-event outcomes reported as total events. The assumptions for these illustrations 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 a stated fraction of the observed effect. These are planning assumptions for the illustrations; the original trial’s sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect if that effect is the true one and the assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. In general, higher planned power requires more participants when the other assumptions stay the same. These figures are not observed power.

Rows describing 100%, 75%, and 50% of the observed effect represent progressively smaller effects to detect. Smaller effects generally require more participants because they are harder to distinguish from random variation. The resulting planning values are illustrations based on the observed contrast and the listed assumptions, not evidence that a future trial would achieve the planned power or reproduce the observed effect.

Very large planning requirements can result when the observed effect is small, because detecting a smaller difference requires greater information. These calculations do not account for unreported features of the original design, potential loss to follow-up, changes in outcome definition, or alternative analysis methods. They should be read as conditional design illustrations rather than recommendations for a particular study.

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 = 0.458; treatment proportion p₁ = 0.333; average p̄ = 0.396.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6916 = 1.3555.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6859 = 0.5773.
4. n = (1.3555 + 0.5773)² / (-0.1250)² = 239.1, rounded up to 240 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 <- 0.458333333333333                          # control proportion
p1 <- 0.333333333333333                          # 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(135811)
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 = 240 (80% power), 320 (90% power)
 75% of observed effect: n per arm = 432 (80% power), 577 (90% power)
 50% of observed effect: n per arm = 983 (80% power), 1,315 (90% power)
power.prop.test: 239.1 
Simulated power at n = 240 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’s posted primary analysis is an odds ratio of 0.59, with a 95% confidence interval from 0.3 to 1.18. The registry does not report the method used for this estimate or a p-value. The simple unadjusted recalculation from the posted counts gives an odds ratio of 0.591, with a confidence interval from 0.296 to 1.179, as well as a risk-difference estimate and an unadjusted p-value. The recalculation is not the sponsor’s analysis and uses posted summary counts rather than any unreported model details.

The sponsor estimate and recalculated odds ratio are close in direction and magnitude, and the discrepancy indicator is false. The sponsor’s own analysis remains the primary reported analysis; a recalculation is best understood as a transparent, unadjusted check based on the summary data, not as a correction or replacement. Their confidence intervals both include the odds-ratio null value of 1, conveying uncertainty around the contrast.

The registry record does not report whether the sponsor analysis adjusted for other factors or used any specific design-based method. Without those details, the source of any small difference between displayed estimates cannot be identified. The reported and recalculated results should be kept distinct when interpreting the evidence.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy, such as an adjustment for testing more than one outcome or a prespecified order for interpreting primary and secondary outcomes. In general, when multiple hypotheses are tested, the chance of at least one apparently unusual result can rise. This is why secondary results are usually interpreted in the context of the original analysis plan and any adjustment for multiple testing. The posted secondary outcome is therefore best treated as additional descriptive evidence, with its unadjusted comparison carrying less weight than a prespecified primary analysis.

Missing-data methods and analysis populations are also not reported in the registry record. The posted primary outcome has counts and denominators for each arm, but the record does not explain whether all randomized participants were included, whether any participants lacked 52-week measurements, or how incomplete visit histories were classified. It does not identify an intention-to-treat, per-protocol, or other analysis population.

These omissions matter because the interpretation of a participant-count endpoint depends on who was included and how missing outcomes were handled. In general, excluding participants with missing outcomes can change the analyzed groups if missingness is related to treatment or outcome status. Different assumptions about missing outcomes can also affect estimates and uncertainty. No missing-data sensitivity analysis is reported in the registry record, so the robustness of the posted comparison to alternative missingness assumptions cannot be assessed.

The original protocol’s statistical analysis plan, including any interim analyses or stopping rules, is not reported in the registry record. This does not establish that such procedures were or were not used; it means their role cannot be evaluated from the posted registry information. Similarly, the reported odds-ratio method is not specified. These reporting gaps limit assessment of whether the posted results match a prespecified analysis and how much flexibility there may have been in choosing among analyses.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalization (27.3%), serious infection requiring hospitalization (13.6%), death (3.0%), serious cv (1.5%), decreased anc (absolute neutrophil count) (1.5%).

The registry posts serious adverse event counts for 17 of 72 participants in the cyclosporin arm and 18 of 66 in the MMF/DEX arm. It also posts other adverse event counts for 50 of 72 and 53 of 66, respectively. The registry lists deaths as 0 in the cyclosporin group and 2 in the MMF/DEX group. These are arm-level counts and denominators as recorded; they should not be interpreted as a complete account of event timing, severity beyond the registry categories, or causal attribution.

The listed serious-event terms include Hospitalization at 27.3%, Serious Infection Requiring Hospitalization at 13.6%, Death at 3.0%, Serious CV at 1.5%, Decreased ANC (absolute neutrophil count) at 1.5%, and Generalized tonic-clonic seizure at 1.4%. The registry does not give additional context for these terms in the posted summary, including event counts by term, overlap between terms, or the denominator used for each listed percentage.

Safety counts are descriptive. They do not by themselves establish that an event was caused by a treatment or allow a reliable comparative safety conclusion. The registry record does not report details such as event timing, seriousness criteria, exposure duration, or an adjusted safety analysis.

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

The posted results describe remission counts in two randomized treatment arms at two time points. At the primary 52-week endpoint, the unadjusted point estimate is in the direction of fewer participants meeting the remission definition in the MMF/DEX arm than in the cyclosporin arm. However, the confidence interval spans the no-difference value, and the posted sponsor odds-ratio interval also includes its null value. The result is therefore uncertain in both direction and magnitude.

This does not establish that the treatments are equivalent. A result with an interval that includes no difference can arise when the data are compatible with no effect, but also when the data are too imprecise to distinguish no effect from meaningful differences in either direction. The registry does not report a formal equivalence or noninferiority design or margin, so the results should not be interpreted as demonstrating equivalence or noninferiority.

Nor does the point estimate alone establish a treatment effect. It is an estimate from the observed counts, subject to sampling uncertainty and to the limitations of the trial’s design and reporting. The open-label design, unreported analysis population, unreported missing-data handling, and absent details about the sponsor’s analysis method all constrain how completely the posted evidence can be assessed.

The 78-week result adds a later observation but does not provide a precise, clear separation between the arms. The secondary result does not independently resolve the primary uncertainty, particularly because the registry record does not report a multiplicity plan or the original analysis hierarchy.

These findings apply to the posted endpoints and reported participant groups. They do not establish effects in populations or settings not described by the registry, explain the reasons for outcome differences, or predict an individual participant’s result. No treatment recommendation follows from these registry statistics alone.

18. Why This Trial Matters Statistically

This trial is statistically informative because it makes a randomized comparison between two treatment strategies for proteinuria remission and reports outcomes at defined follow-up times. The endpoint is operationalized through urine protein/creatinine thresholds and ordered score categories, allowing the primary comparison to focus on participants meeting a stated remission definition rather than on an unspecified clinical impression.

It also illustrates why point estimates, confidence intervals, and analysis provenance need to be read together. The direction of a point estimate is not the same as certainty about a treatment contrast. Here, the posted intervals span the null values, so the data do not precisely establish the direction or magnitude of a difference. The sponsor’s odds ratio and the unadjusted recalculation are related summaries, but they are not interchangeable analyses.

The trial also highlights the importance of registry reporting beyond headline results. Details about the analysis population, missing outcomes, multiplicity, statistical methods, and sample-size rationale would help readers judge how the posted estimates relate to the original plan. Their absence does not invalidate the counts, but it limits evaluation of potential analytic choices and the robustness of conclusions.

Finally, the sample-size illustrations demonstrate a general design principle: smaller effects require larger samples to detect under the same assumptions. They should not be confused with the trial’s design justification or with evidence that the trial had a particular level of observed power. Separating planned design assumptions, posted findings, and post hoc recalculations is essential to sound interpretation.

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.

Several limitations specific to the registry record affect interpretation. The study is open label, and the record does not say whether outcome assessors were masked. Although the remission outcome uses defined thresholds and time points, details about measurement procedures and adjudication are not reported.

The primary outcome denominators are 72 and 66, while total enrollment is listed as 192. The registry record does not explain the relationship between enrollment and the denominators contributing to the posted outcome counts. It also does not report how participants with missing measurements or incomplete follow-up were handled, which analysis population was used, or whether outcome data were available for all randomized participants.

The method behind the sponsor’s odds ratio is not reported, and the sponsor result has no posted p-value. The original statistical analysis plan, multiplicity strategy, interim analyses, and sample-size justification are also not reported in the registry record. These gaps make it difficult to assess whether the displayed analyses were prespecified and how they account for the trial design.

The secondary result is unadjusted in the recalculation, and the registry record does not describe how multiple outcomes were intended to be interpreted. The safety summary provides counts and selected event terms but not the detail needed to assess timing, overlapping events, exposure, or causal attribution. These limitations concern the completeness of the posted information; they do not imply that unreported procedures were absent from the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Focal Segmental Glomerulosclerosis Clinical Trial (FSGS-CT) — NCT00135811.
• Registry record last updated 2026-09-18; status last verified 2026-08.
• Results first posted 2026-09-18.
• 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

NCT00135811, the Focal Segmental Glomerulosclerosis Clinical Trial (FSGS-CT), is listed as a completed phase 3 randomized, parallel, open-label study sponsored by NIDDK. It compared cyclosporin with MMF/DEX and recorded enrollment of 192. The primary outcome was partial or complete proteinuria remission at 52 weeks, with remission at 78 weeks listed as a secondary outcome.

The primary posted counts favor cyclosporin in the unadjusted point estimate, but the reported uncertainty includes no difference. The secondary comparison is also imprecise and does not resolve the primary uncertainty. The registry record does not report important details of the original analysis plan, missing-data handling, or multiplicity approach. The results are best read as estimates with substantial uncertainty and limits in the available methodological reporting.