N-Acetylcysteine and Milk Thistle for Treatment of Diabetic Nephropathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for N-Acetylcysteine and Milk Thistle for Treatment of Diabetic Nephropathy (NCT01265563), a randomized phase 2 study. The primary outcome is Change From Baseline in Urinary Albumin Excretion.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, triple-masked, parallel-group study sponsored by the VA Office of Research and Development. The registry records enrollment of 108 and a completed status. The study began in 2011-01, with primary completion in 2015-02. The trial's title concerns N-acetylcysteine and milk thistle for diabetic nephropathy; its official title describes correction of glutathione deficiency for treatment of diabetic nephropathy.

Five treatment groups are listed: placebo for both supplements; active NAC with silibin placebo; NAC placebo with active silibin; active NAC with active silibin; and active NAC with higher-dose active silibin. The primary outcome results are posted for all five groups. Each comparison reported is between one active regimen and the double-placebo control. The registry does not report direct statistical comparisons among the active regimens, so the results do not directly test whether adding one supplement to another improves the endpoint beyond either component alone.

Randomization means assignment was intended to be determined by chance, while triple masking indicates that the registry classifies the study as masked at three levels. The identities of those masked and the allocation procedure are not reported in the registry record. The registry also does not report the planned allocation ratio, the original target sample size, or the trial's original sample-size assumptions. The recorded enrollment and the numbers contributing to the outcome groups are distinct pieces of information; the outcome summaries have group-specific participant counts.

The primary outcome timeframe was baseline and 3 months. The registry lists change in hemoglobin-A1c and urinary alpha-1 microglobulin, inflammatory cytokines, and C-C chemokines as secondary outcomes. Only two secondary outcome records are posted with group summaries, and no reported analyses are listed for them. The protocol details, including the full analysis population definition and handling of missing endpoint observations, are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: During Run-in phase before randomization to the experimental arms, 4 subjects were excluded due to hospitalization for various reasons and 26 were excluded due to issues with transportation or sickness in the family or themselves.

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 Change From Baseline in Urinary Albumin Excretion, measured over Baseline and 3 months.

The primary endpoint is change from baseline in urinary albumin excretion, measured by the urine albumin-to-creatinine ratio and expressed in mg/g. The registry describes assessment at the end of the run-in period and after 3 months of study intervention. A change score represents the difference between a participant's follow-up measurement and their baseline measurement; group means describe the average change among participants represented in each group.

Urinary albumin is used in this study as a measure related to protein loss in urine, a feature of diabetic kidney disease. The stated research purpose was to examine whether the supplement regimens affected protein shedding and oxidative damage. This endpoint therefore addresses a biological measure relevant to the study question, but it is not itself a direct measure of how a participant feels or functions, nor does it by itself establish a long-term clinical outcome.

The spread reported for each group is a standard deviation, which describes variation in individual change scores around the group mean. The posted groups have substantial variability relative to their average changes, and the comparisons consequently have broad confidence intervals. A group mean can be positive or negative while individuals within the group vary in either direction. Interpretation should therefore consider both the estimated mean change and the uncertainty around the comparison, rather than treating the group average as a description of every participant.

The endpoint is continuous, so the posted comparison is expressed as a mean difference between an active regimen and the placebo group. Positive and negative changes describe opposite directions of change in the measured ratio; the posted summary alone does not establish the clinical importance of a particular change.

7. Results Posted in the Registry

• NAC Active + Silibin Placebo: mean -28.13 versus 50.50 on control; difference -78.63 (95% CI -435.60 to 278.34), standardized effect d = -0.18; z-test p = 0.666.
• NAC Placebo + Silibin Active: mean -4.50 versus 50.50 on control; difference -55.00 (95% CI -356.05 to 246.05), standardized effect d = -0.13; z-test p = 0.720.
• NAC Active + Silibin Active: mean 96.60 versus 50.50 on control; difference 46.10 (95% CI -205.29 to 297.49), standardized effect d = 0.13; z-test p = 0.719.
• NAC Active + High-dose Silibin Active: mean 353.71 versus 50.50 on control; difference 303.21 (95% CI -106.24 to 712.66), standardized effect d = 0.56; z-test p = 0.147.

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.

Change From Baseline in Hemoglobin-A1c

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • NAC Active + Silibin Placebo: mean -0.18 versus 0.35 on control; difference -0.53 (95% CI -1.01 to -0.05), standardized effect d = -0.85; z-test p = 0.030.
  • NAC Placebo + Silibin Active: mean 0.72 versus 0.35 on control; difference 0.37 (95% CI -1.08 to 1.82), standardized effect d = 0.18; z-test p = 0.618.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for NAC Active + Silibin Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NAC Placebo + Silibin Active and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context but do not resolve the uncertainty in the primary endpoint. The registry lists change in hemoglobin-A1c and urinary alpha-1 microglobulin, inflammatory cytokines, and C-C chemokines. Posted summaries are available for hemoglobin-A1c and for urinary alpha-1 microglobulin, inflammatory cytokines, and C-C chemokines as a grouped outcome description, but reported comparison analyses are limited. No reported analyses are listed for the secondary outcome records.

Across the posted secondary summaries, group changes vary by treatment and measure. Their scale and spread are not uniform, and some group summaries show appreciable dispersion. This variation reinforces the need to treat secondary measures as exploratory descriptions rather than as a consistent pattern that independently confirms the primary endpoint. The secondary results do not establish that changes in one biological measure explain changes in another.

The secondary measures relate to the study's broad interest in diabetic kidney disease, metabolic control, and biological processes. They are not interchangeable with the primary urinary albumin-to-creatinine outcome. A result on a secondary measure cannot be used as a substitute for a clear primary comparison, nor can it establish a longer-term clinical effect. The registry record does not report a prespecified hierarchy connecting these outcomes or an analysis plan for interpreting them jointly.

Unadjusted secondary results carry less weight because several outcomes and comparisons create multiple opportunities for apparently notable findings. Without a reported multiplicity plan, isolated estimates or p-values may overstate how much evidence they represent. The registry record does not report multiplicity-adjusted secondary analyses. The prudent interpretation is that these outcomes are supplementary and hypothesis-generating, and that their pattern should be considered alongside—not instead of—the imprecise primary results.

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

• Change From Baseline in Hemoglobin-A1c
• Urinary Alpha-1 Microglobulin, Inflammatory Cytokines and C-C Chemokines

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary results summarize a continuous outcome using a mean and standard deviation in each treatment group. A mean is the arithmetic average of the observed changes; the standard deviation describes how dispersed those observations are around the mean. Because participants can have quite different changes, the standard deviation is important context: a mean alone does not reveal how much individual responses varied.

What does a mean difference represent?

Each reported comparison subtracts the control-group mean change from the mean change in one active group. A negative estimate means that the active group's average change was lower than the control group's average change, while a positive estimate means it was higher. The sign describes the direction of the numerical contrast, not whether the result is beneficial or harmful. That interpretation depends on the endpoint's clinical meaning and cannot be established solely by the sign of the estimate.

The reported comparisons are unadjusted mean differences. The posted summaries also include a pooled standard deviation and a standardized effect estimate, but the clinical-unit mean difference is generally easier to interpret directly: it remains in mg/g. Standardization expresses a mean difference relative to within-group variability and can aid comparison across measures with different units. It does not remove uncertainty or make a small study more informative.

How should confidence intervals be read?

A confidence interval is a range of estimates compatible with the observed data under the assumptions of the statistical method. It conveys precision as well as the direction and size of the estimated difference. A narrow interval would indicate greater precision; a wide interval indicates that the data leave substantial uncertainty. For the primary comparisons, all posted intervals span zero and include differences on both sides of zero. This means the results do not precisely distinguish a difference in one direction from a difference in the other direction.

A confidence interval is not a list of likely values for every participant, and it is not a guarantee that the true effect lies inside the specific interval. It is also not a substitute for clinical judgment about what size of change would matter. The registry does not report a threshold for clinical importance for this endpoint, so the clinical interpretation of a particular point estimate cannot be determined from the posted results alone.

What does an unadjusted p-value tell us?

The p-value summarizes how unusual data at least as incompatible with a no-difference hypothesis would be under the statistical model and assumptions used for the test. It does not give the probability that the null hypothesis is true, and it does not quantify the chance that a result is due to chance. The posted primary p-values are unadjusted. With several active-versus-control comparisons, unadjusted values do not account for the fact that multiple hypotheses are being examined. The registry record does not report a multiplicity strategy or identify a single comparison as the sole confirmatory test.

A p-value should be read together with the effect estimate and confidence interval. In particular, a large p-value does not show that two regimens have equivalent effects. Establishing equivalence or excluding meaningful differences would require suitable prespecified margins and an analysis designed for that purpose; those are not reported in the registry record.

Why does variability matter?

The standard deviations are large relative to the group mean changes, and the group sizes are limited. High variability makes it harder to estimate a group contrast precisely because individual measurements differ considerably. It can also make estimates more sensitive to a small number of observations. The registry does not provide participant-level data or distribution plots in the record described, so the shape of the outcome distributions, the influence of extreme values, and the presence of skew cannot be assessed from the group summaries alone.

Urinary measurements may show substantial between-person variation as a general statistical consideration. General methods such as transformation, robust estimation, or nonparametric comparison can sometimes be considered when distributional assumptions are uncertain, but the registry record does not report whether these methods were planned or used. No alternative analysis should be inferred from the summary statistics.

What can the posted analysis establish?

The registry posts group means, standard deviations, mean differences, confidence intervals, and unadjusted p-values for comparisons with the placebo group. It does not list reported analyses in the primary comparison record. The statistical plan, model specification, covariate adjustment, approach to missing observations, and definition of the analysis population are not reported in the registry record. The posted numbers can describe the reported summary contrasts, but they do not reveal all decisions behind the analysis or establish whether assumptions were checked.

Random assignment supports a comparison of groups, but a reliable interpretation also depends on how the trial was conducted and analyzed. Masking and randomization are design features; they do not by themselves guarantee precise estimates. The small outcome-group counts and broad intervals remain central when judging how much information these results provide.

11. Confidence Intervals and Precision

The primary comparisons are imprecise. Their confidence intervals extend across zero and cover a broad range of possible mean differences. For NAC active plus silibin placebo, the estimate is -78.63 mg/g with a confidence interval from -435.6 to 278.3 mg/g. The estimate for NAC placebo plus silibin active is -55.0 mg/g, with an interval from -356.0 to 246.0 mg/g. These intervals allow for differences in either direction and do not pin down a narrow effect range.

The combination of active NAC and active silibin has an estimated difference of 46.1 mg/g, with a confidence interval from -205.3 to 297.5 mg/g. The NAC active plus high-dose silibin active comparison has an estimated difference of 303.2 mg/g, with a confidence interval from -106.2 to 712.7 mg/g. Although the point estimates differ, the intervals overlap broadly and include zero. The point estimates alone should not be used to rank the regimens.

Precision is limited in part by the small number of participants contributing to each primary-outcome group: group counts range from 12 to 16. The observed standard deviations are also substantial. Together, these features mean that the posted estimates do not exclude potentially important changes in either direction. The registry does not report a clinical threshold against which to judge the interval limits, so it is not possible to determine from this record whether any range of values would be clinically negligible.

Confidence intervals express uncertainty about estimated group differences, not the range of individual responses. The posted intervals also do not account for uncertainty arising from choices not described in the registry record, such as analysis-population definitions or missing-data handling. The most defensible reading is that the primary comparisons are uncertain and not sufficiently precise to support a firm conclusion about the size or direction of the differences.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, rather than the trial's original design assumptions. For these continuous-outcome comparisons, the figures are participants per arm, not total events. The planning assumptions 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 to the stated fraction of the observed effect. The original design assumptions for the trial are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a future comparison to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the planning model were correct. The 90% power column gives the corresponding planning number for a higher chance of detecting that effect. These are prospective planning quantities, not probabilities that the posted trial result is correct and not a measure of how likely the observed result was to be detected.

Rows planning for 100%, 75%, and 50% of the observed effect consider progressively smaller effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same planning assumptions. This pattern is visible across the comparisons: the illustrations for smaller fractions call for larger group sizes. The numerical estimates vary across comparisons because each observed effect and its variability differ.

These figures are not observed power. They are not a retrospective explanation of the trial's results and should not be used to infer that an outcome was or was not detected because the actual groups were smaller than an illustrative target. They also do not account for possible features of the original trial design that are not reported in the registry record.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -78.630; pooled standard deviation σ = 436.373.
2. n = 2 × (1.96 + 0.842)² × 436.373² / -78.630² = 483.5, rounded up to 484 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
delta <- -78.63                      # observed difference in means
sigma <- 436.372981184322                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1265563)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 484 (80% power), 648 (90% power)
 75% of observed effect: n per arm = 860 (80% power), 1,151 (90% power)
 50% of observed effect: n per arm = 1,934 (80% power), 2,589 (90% power)
power.t.test: 484.4 
Simulated power at n = 484 per arm: 0.798 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists several treatment groups, a primary endpoint, and secondary outcomes, but the statistical plan for handling multiple comparisons is not reported in the registry record. Each posted primary comparison is against the same placebo group, and the reported p-values are unadjusted. When multiple hypotheses are tested, the chance of at least one apparently unusual result can rise; adjustment or a prespecified testing hierarchy can address this issue. Neither approach is described in the record, so the unadjusted p-values should not be interpreted as if they came from a single isolated test.

The registry also does not report whether the primary comparison was designated as a single main contrast among the active groups, whether any outcomes were exploratory, or whether the reported comparisons followed a prespecified hierarchy. Direct tests among active regimens are not posted. These omissions limit how confidently the numerical findings can be placed within the trial's original inferential plan.

Missing-data procedures and the analysis population are not reported in the registry record. It is not stated whether the summaries include all randomized participants, participants who completed the intervention, or another defined group. The group-specific endpoint counts are posted, but the reasons participants may not contribute an endpoint and the methods, if any, used to address missing measurements are not described. Consequently, it is not possible to assess from this record whether missingness could have affected the group comparisons.

Other analysis details are also unavailable, including covariate adjustment, model choice, assumption checks, and any planned interim analyses. These should not be inferred from the posted means and confidence intervals. The absence of these details does not prove that the trial lacked such procedures; it means their use and rationale are not reported in the registry record. This uncertainty matters when interpreting unadjusted estimates from a small set of groups and outcomes.

15. 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: chest pain (8.3%), bradycardia (7.1%), wheezing (6.2%), motor vehicle accident (6.2%), osteomyelitis (6.2%).

The registry reports serious adverse events for participants at risk in each treatment group. One participant in each group is listed as affected by a serious adverse event. The number at risk differs by group, and the record also lists zero deaths in every group. These are counts from the posted safety summaries; they do not by themselves establish whether an event was caused by a study supplement.

The registry lists chest pain, bradycardia, wheezing, motor vehicle accident, and osteomyelitis among the leading serious adverse-event terms, with percentages of 8.3%, 7.1%, 6.2%, 6.2%, and 6.2%, respectively. These terms should be read as event listings, not as evidence that the interventions caused them. The record does not provide enough detail in these summaries to determine event timing, relatedness assessments, recurrence, or differences in exposure time.

Safety comparisons are difficult to interpret when group sizes are small. The counts describe what was recorded during the trial, but they cannot establish that risks are equal across regimens or that a serious event is absent from a group beyond the listed count. The registry record does not report a detailed causal assessment or a statistical comparison of adverse events.

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

The primary results describe observed changes in urinary albumin excretion over the registry's baseline-to-3-month timeframe and compare the mean change in each active-regimen group with the mean change in the placebo group. The point estimates vary in direction and size, and the confidence intervals are broad. This combination indicates uncertainty about both the direction and magnitude of the group differences.

The posted data do not establish that any regimen produces a particular change, and they do not establish that the groups are equivalent. A non-significant unadjusted p-value is not proof of no effect. Conversely, a point estimate in one direction is not sufficient evidence that the regimen caused that difference. The study's small endpoint group counts and substantial variation limit the precision of the estimates.

The results also do not establish that combining NAC and silibin has an effect beyond either supplement alone. The reported comparisons are active regimen versus double-placebo, not direct tests between active regimens or a formal test of interaction. Any apparent differences between the active-group means are descriptive unless supported by appropriately designed and reported statistical comparisons.

The trial concerns short-term biological measures. The primary endpoint is urinary albumin-to-creatinine ratio change, and the posted timeframe is 3 months. The record does not establish effects on longer-term kidney outcomes, symptoms, function, or other clinical outcomes. It also does not report a threshold for a clinically important difference in the primary measure. Thus, the statistical estimates should not be converted into treatment advice or claims about clinical benefit.

The best-supported conclusion from this registry record is limited: it reports variable group mean changes and imprecise, unadjusted comparisons with the placebo group. The intervals include differences in either direction, and the available registry entries do not resolve the uncertainty. More detailed analyses or additional evidence would be needed to characterize the size, consistency, and clinical importance of any effect.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of the distinction between an observed point estimate and a precise estimate. Several group means differ numerically, but the uncertainty around the active-versus-control comparisons is substantial. Reading the mean differences alongside their confidence intervals prevents overinterpreting isolated values or treating a non-significant p-value as evidence of equivalence.

The five-group structure also illustrates the difference between a set of comparisons against a shared control and direct comparisons among active regimens. The posted estimates can describe how each regimen compares numerically with placebo, but they do not determine whether one active regimen outperforms another or whether the supplements interact. That distinction is important whenever a trial includes multiple components or dose combinations.

The registry record highlights how variability and limited group counts affect precision. Standard deviations are large, and each primary-outcome group contains relatively few participants. Even when a trial is randomized and masked, design features cannot eliminate uncertainty caused by limited information. Randomization supports fair comparisons in principle; it does not guarantee that an estimate will be narrow or that a modest effect can be distinguished reliably.

Finally, the record demonstrates why transparency about analysis plans matters. Multiplicity handling, missing-data methods, analysis populations, and the original sample-size justification are not reported. Their absence from the registry record makes it harder to evaluate how the posted analyses relate to the trial's original aims. Clear reporting of these choices helps readers distinguish planned tests from exploratory findings and understand the limits of the evidence.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to this registry record constrain interpretation. The primary outcome groups contain 12 to 16 participants, and the standard deviations are large. The resulting confidence intervals are broad, leaving substantial uncertainty about the differences that may be compatible with the observed data. The study is listed as phase 2, and the registry does not report a design justification that would clarify the intended precision of the trial.

The record lists five groups, but the posted primary comparisons are only active regimen versus the double-placebo group. It does not report direct comparisons among active regimens or an interaction analysis for NAC and silibin. Therefore, the results do not answer whether the combination differs from its individual components. Nor is a dose-response analysis reported for silibin.

The outcome is measured over baseline and 3 months. The registry does not report longer-term follow-up for this endpoint, nor does it establish how a change in this biological measure relates to clinical outcomes. No clinical-importance threshold is reported. The record also does not provide participant-level distributions, making it difficult to assess skew, influential observations, or other features that could affect a mean-based analysis.

Important analysis details are not reported in the registry record, including the analysis population, missing-data approach, covariate adjustment, model assumptions, multiplicity procedures, and any interim analyses. The number enrolled is recorded, but the reasons for differences between overall enrollment and outcome-group counts are not described. These gaps do not establish that the procedures were absent; they limit what can be evaluated from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: N-Acetylcysteine and Milk Thistle for Treatment of Diabetic Nephropathy — NCT01265563.
• Registry record last updated 2018-10-19; status last verified 2018-09.
• Results first posted 2017-03-31.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01265563 is a completed phase 2 randomized, triple-masked, parallel-group trial sponsored by the VA Office of Research and Development, with enrollment of 108. It evaluated placebo and active combinations of N-acetylcysteine and silibin, including a higher-dose silibin regimen, for diabetic nephropathy.

The primary endpoint was change in urinary albumin excretion, measured by the urine albumin-to-creatinine ratio at baseline and 3 months. The registry reports group means, standard deviations, and active-versus-placebo mean differences. Those comparisons have broad confidence intervals that include zero, and their p-values are unadjusted.

The posted results are therefore imprecise and do not establish a clear difference between any active regimen and the placebo group. The registry record does not report the original sample-size assumptions, a multiplicity plan, missing-data methods, or a detailed statistical analysis plan. Secondary outcomes and adverse-event summaries provide additional context but do not remove the uncertainty in the primary comparisons.