Low Dose Versus Aggressive Inhibition of the Renin-Angiotensin-Aldosterone (RAS) to Treat Microalbuminuria: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Low Dose Versus Aggressive Inhibition of the Renin-Angiotensin-Aldosterone (RAS) to Treat Microalbuminuria (NCT00907374), a randomized na study. The primary outcome is Microalbuminuria Reported as Urinary Albumin:Creatinine Ratio.

2. Clinical Question

The study summary also describes interest in estimated glomerular filtration rate, endothelial dysfunction measured by post-hyperemia arterial tonometry, and atherosclerotic disease progression measured by carotid intima media thickness. These outcomes offer additional measures related to kidney function, vascular function, and arterial structure, but they do not change the definition of the primary endpoint.

The posted primary means are 256.1 for low-dose inhibition and 376.2 for aggressive inhibition. The estimated mean difference, aggressive minus low dose, is 120.1. The confidence interval is broad and spans values on either side of no difference. The results therefore describe the observed data with substantial uncertainty; they do not, on their own, establish that one regimen is superior or that the regimens are equivalent.

3. Trial Design

The registry describes a randomized, parallel-group study with no masking. Its status is completed, and its listed enrollment is 46. The phase is recorded as NA. The sponsor is Charles Drew University of Medicine and Science. The study began in 2005-07, and primary completion is listed as 2009-04.

Random allocation is intended to make the treatment groups comparable on average, including with respect to factors that may affect outcomes. It cannot guarantee that groups will be alike in a small trial, and the record does not report details about the randomization sequence or allocation concealment. With no masking, participants and study personnel were not blinded to group assignment according to the registry designation. The record does not describe whether outcome assessors were masked.

The parallel design means participants were assigned to one of the two regimens rather than being described as crossing between them. The low-dose arm used 10 mg benazepril orally daily. The aggressive-inhibition arm used 40-80 mg benazepril plus 25-100 mg losartan, both orally once or twice daily. The registry lists benazepril as the drug intervention in both entries; the aggressive arm description also names losartan.

Although the registry lists enrollment of 46, the primary endpoint results give group counts of 12 and 11, while the safety figures use at-risk counts of 14 and 13. These are the denominators attached to their respective posted results. The registry record does not explain why the counts differ, whether the endpoint counts reflect a particular analysis population, or what happened to participants without posted endpoint values. It is not possible to infer the reason from the record alone.

The registry describes an intended assessment of progression of microalbuminuria, estimated glomerular filtration rate, endothelial dysfunction, and carotid intima media thickness. The primary endpoint timeframe is 3 to 36 months, and the two vascular secondary outcome timeframes are 6 to 36 months. The specific visit schedule, adherence procedures, and detailed protocol 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: 46 patients were enrolled and entered the run-in but 19 were not 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 Microalbuminuria Reported as Urinary Albumin:Creatinine Ratio, measured over 3 to 36 months.

The primary endpoint is microalbuminuria reported as urinary albumin:creatinine ratio. It is a continuous measure, and the registry reports an arithmetic mean and standard deviation for each arm. The posted value is described as the average of the ratio for all participants during months 3 to 36. The unit is recorded as Ratio.

Urinary albumin measured relative to creatinine is used to express albumin excretion in relation to urine concentration. In general, this kind of measure can help assess albuminuria while accounting for variation in how concentrated a urine sample is. That general rationale does not establish how samples were collected or how the measure was processed in this study; those details are not reported in the registry record.

Using a continuous endpoint preserves information across the observed range rather than reducing the measure to categories. The mean describes the group’s average, while the standard deviation describes how widely individual values vary around that average. Both are important for interpretation: a difference between means is easier to judge when the within-group variation and uncertainty around the difference are also considered.

The endpoint description specifies averaging over the 3 to 36 months of the study, but it does not explain the participant-level calculation, such as how repeated measurements were combined or how missing visits were handled. Those methods are not reported in the registry record. The posted mean should therefore be interpreted as the registry’s stated average outcome, without assuming a particular repeated-measures model or missing-data procedure.

7. Results Posted in the Registry

• Agressive Inhibition of the RAS: mean 376.20 versus 256.10 on control; difference 120.10 (95% CI -319.52 to 559.72), standardized effect d = 0.22; z-test p = 0.592.

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.

Estimated Glomerular Filtration Rate

• 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:
  • Agressive Inhibition of the RAS: mean 100.50 versus 108.70 on control; difference -8.20 (95% CI -31.57 to 15.17), standardized effect d = -0.29; z-test p = 0.492.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Agressive Inhibition of the RAS and the control. The interval gives the range of effects that remain compatible with the data.

Carotid Artery Intima Thickness

• 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:
  • Agressive Inhibition of the RAS: mean 0.72 versus 0.74 on control; difference -0.02 (95% CI -0.13 to 0.09), standardized effect d = -0.15; z-test p = 0.728.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Agressive Inhibition of the RAS and the control. The interval gives the range of effects that remain compatible with the data.

Endothelial Dysfunction

• 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:
  • Agressive Inhibition of the RAS: mean 2.00 versus 2.20 on control; difference -0.20 (95% CI -0.70 to 0.30), standardized effect d = -0.33; z-test p = 0.434.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Agressive Inhibition of the RAS and the control. The interval gives the range of effects that remain compatible with the data.

The three secondary outcomes cover estimated glomerular filtration rate, carotid artery intima thickness, and endothelial dysfunction. Their posted comparisons are also mean differences with confidence intervals and unadjusted p values. Across these measures, the intervals span zero and extend in both directions. Taken together, the secondary results do not provide a precise pattern that removes uncertainty around the primary endpoint.

These outcomes complement the primary urinary albumin:creatinine ratio by representing kidney function and vascular measures identified in the study objective. They may provide context about different aspects of the intended assessment, but they are not interchangeable with the primary measure. A result on one does not automatically confirm or refute a result on another, particularly when the outcomes capture different biological measures and have different observation timeframes.

The registry record lists three secondary outcomes and four outcome measures, but does not report a multiplicity strategy. When several outcomes are examined, the chance of observing at least one apparently notable result can increase. A prespecified hierarchy or adjustment can address that issue, but none is described in the registry record. The secondary p values should therefore be treated as exploratory or descriptive rather than as a set of independent confirmatory tests.

The record also does not list formal reported-analysis entries for the secondary outcomes. The posted summaries permit description of group means and unadjusted contrasts, but do not reveal whether analyses were prespecified, adjusted for baseline values, or based on all randomized participants. The secondary findings consequently carry less inferential weight than a fully reported, prespecified analysis with a stated multiplicity plan. They should be viewed as additional, uncertain evidence rather than as independent conclusions about the treatment comparison.

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

• Estimated Glomerular Filtration Rate
• Carotid Artery Intima Thickness
• Endothelial Dysfunction

9. Statistical Interpretation

10. Statistical Methods Explained

The registry posts continuous outcomes as means with standard deviations, together with arm comparisons expressed as mean differences, confidence intervals, and unadjusted p values. The explanations below are general statistical context; details of the trial’s original analysis plan are not reported in the registry record.

What does a mean difference represent?

A mean is the arithmetic average of the recorded values within a group. A mean difference compares two such averages. For the primary outcome, the comparison is aggressive inhibition minus low-dose inhibition, so a positive estimate means the posted aggressive-inhibition mean is higher. A negative estimate would mean it is lower. The estimated difference is 120.1, matching the direction implied by the two posted means, 376.2 and 256.1. No new calculation is needed to interpret that direction.

A difference between means is a summary of group averages, not a description of every participant’s result. It can conceal variation within groups or changes in outcome over time. In this study the primary endpoint is described as an average over months 3 to 36, but the registry does not report whether that average represents a participant-level average of repeated measures or another procedure.

Why report standard deviations?

In general, the standard deviation describes the spread of values around a group mean. It is not the uncertainty in the mean difference itself, and it is not a confidence interval. The primary outcome standard deviations are 652.3 for the low-dose arm and 404.2 for the aggressive-inhibition arm. These measures indicate substantial variability in the posted outcome values. When variation is large relative to the difference between group means, the data may be consistent with a broad range of plausible mean differences.

A standard deviation can also be affected by unusual high or low values, particularly for measures whose values vary widely. The registry record does not report distributions, medians, ranges, transformations, or checks of model assumptions. It is therefore not possible to assess from the posted summaries whether the outcome values were symmetric or whether a different summary would have been informative.

How should a confidence interval be read?

In general, a confidence interval gives a range of values compatible with the data under the statistical procedure used. It expresses uncertainty around an estimate, rather than listing the range of individual participant values. The primary interval is -319.5 to 559.7. Because it includes zero and extends in both directions, it does not precisely determine the sign or size of the underlying difference.

The interval is not a guarantee that the true effect lies inside its endpoints, nor does it assign a probability to a specific value after the data have been observed. Its interpretation depends on the analysis and assumptions used to construct it. The registry record does not identify the specific procedure used to calculate the intervals, so a particular test or interval method should not be assumed.

What does an unadjusted p value say?

In general, a p value measures how unusual results at least as different as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, the probability that the finding is due to chance, or a measure of clinical importance. The primary unadjusted p value is 0.592. It does not by itself establish equality, and it does not tell how large or important a difference might be.

“Unadjusted” matters because the posted value is not identified as accounting for multiple outcomes, covariates, or other analyses. No adjustment method is reported. The mean differences and p values should therefore be read as unadjusted comparisons, not as evidence from a documented adjusted model. Whether any analysis was performed outside the registry is not reported in the registry record.

What can be inferred from randomization?

In general, random allocation supports comparison by reducing systematic differences in treatment assignment. It does not ensure that all prognostic characteristics will be balanced in a small study. The registry records random allocation, but does not report the sequence-generation procedure, concealment method, baseline characteristics, or analysis preserving randomized assignment. No claim about these procedures or the resulting balance can be made from the record.

The parallel design assigns participants to one of the two regimens. The study was unmasked, so the registry does not describe a blinded treatment assignment. Lack of masking can matter for outcomes involving participant behavior, measurement, or decisions; the extent to which it affected this study is not reported. The record also does not say whether outcome assessors were masked separately.

What analysis details remain unknown?

The registry reports four outcome measures and three secondary outcomes. It does not list formal reported analyses for the secondary endpoints. The analysis population, treatment of missing values, use of baseline adjustment, handling of repeated observations, and any correction for multiple testing are not reported in the registry record. The registry also does not report the trial’s original statistical analysis plan or the method used to calculate its confidence intervals and p values.

Those omissions limit the ability to reproduce or evaluate the analyses. For example, if repeated observations were available, different approaches could account for within-participant correlation differently. If some outcomes were missing, different handling strategies could affect the estimates. These are general methodological considerations, not claims about what was done in this trial.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a quantity, not whether the estimate is important. For the primary mean difference, the estimate is 120.1 and the 95% confidence interval runs from -319.5 to 559.7. That interval is broad and includes zero, as well as values favoring either comparison direction. It therefore leaves considerable uncertainty about both the direction and magnitude of the underlying difference.

The primary arm means are 256.1 and 376.2, with standard deviations of 652.3 and 404.2. The large spread of participant values relative to the difference between means is consistent with the wide uncertainty in the contrast. The endpoint group counts are 12 and 11. These are the counts attached to the primary outcome results; the record does not explain how they relate to the listed enrollment.

A confidence interval spanning zero is not a demonstration of equivalence. Equivalence requires a prespecified margin defining differences small enough to regard as practically similar, alongside a suitable analysis. No equivalence margin is reported in the registry record. Nor does the interval show that no meaningful difference is possible: its endpoints include a substantial range of values.

The p value of 0.592 is consistent with an imprecise comparison, but it should not replace the interval when judging precision. The interval makes clear that the data do not tightly constrain the possible difference. The registry record does not report a clinically important threshold against which the estimate could be assessed, so statistical uncertainty cannot be translated into a conclusion about clinical importance.

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 estimates are illustrative calculations based on the observed effect, not a record of the study’s original design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. The figures are participants per arm, not total participants or total events.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the selected effect under those assumptions, if that effect and the calculation assumptions held. The 90% power column gives the corresponding planning estimate for a higher chance of detection. These are planning illustrations, not observed power.

For the primary comparison, the estimates increase as the assumed effect becomes smaller: planning for 100% of the observed effect gives 328 participants per arm for 80% power and 439 for 90% power; planning for 75% of the observed effect gives 582 and 779; planning for 50% of the observed effect gives 1,309 and 1,753. This pattern is expected in general: smaller effects are harder to distinguish from random variation and require more participants under otherwise similar assumptions.

The trial’s own original sample-size justification and design assumptions are not reported in the registry record. The observed enrollment and outcome counts should not be read as demonstrating that the study had adequate power for the primary or secondary outcomes. A calculation based on an observed estimate can also be unstable when the estimate is uncertain, as it is for the primary outcome. It is best understood as a hypothetical planning aid, not as a retrospective verdict on the 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 120.100; pooled standard deviation σ = 548.341.
2. n = 2 × (1.96 + 0.842)² × 548.341² / 120.100² = 327.2, rounded up to 328 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 <- 120.1                      # observed difference in means
sigma <- 548.340552420274                     # 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(907374)
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 = 328 (80% power), 439 (90% power)
 75% of observed effect: n per arm = 582 (80% power), 779 (90% power)
 50% of observed effect: n per arm = 1,309 (80% power), 1,753 (90% power)
power.t.test: 328.2 
Simulated power at n = 328 per arm: 0.801 (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 identifies one primary endpoint and three secondary outcomes, but does not report a multiplicity plan. Multiplicity refers to the statistical issue created when several outcomes or hypotheses are examined: even if each test is conducted in the usual way, considering many tests can increase the chance of a nominally notable result. A prespecified hierarchy, adjustment, or explicitly exploratory interpretation can help clarify how to read such findings. None is documented in the registry record.

The posted p values are unadjusted. No family-wise error procedure, false-discovery procedure, hierarchical testing sequence, or other correction is reported. This absence does not show that no plan existed outside the registry; it means the registry record does not document one. Secondary findings should consequently not be treated as confirmatory evidence based solely on their individual unadjusted comparisons.

Missing-data methods are also not reported in the registry record. The primary results have endpoint group counts of 12 and 11, while the registry lists enrollment of 46 and the safety figures give at-risk counts of 14 and 13. The record does not state why these denominators differ, how many measurements were missing, whether participants withdrew, or whether the endpoint summaries use a complete-case population. No assumptions about missingness or imputation can be made.

The analysis population is not reported. In particular, the record does not say whether the comparison was based on all randomized participants, participants who received treatment, participants with outcome data, or another defined group. It also does not report whether treatment assignment was retained for analysis regardless of adherence. These details affect how closely an analysis reflects the randomized comparison and how broadly its results can be interpreted.

The statistical model and adjustment strategy are not described. The registry does not report whether baseline outcome values or other covariates were included, how repeated measurements were handled, or how confidence intervals and p values were calculated. The trial’s original protocol, analysis plan, and sample-size justification are not reported in the registry record. These gaps limit reproducibility and prevent a complete assessment of prespecification, missingness, and the inferential status of secondary results.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events among 14 at risk in the low-dose arm and zero among 13 at risk in the aggressive-inhibition arm. It lists zero other adverse events among 14 at risk in the low-dose arm and 2 among 13 at risk in the aggressive-inhibition arm. These are the posted counts and denominators; they should not be conflated with the endpoint group counts.

These figures describe events recorded in the registry, not a complete account of all possible harms or the likelihood of an event outside the study. The record lists no serious adverse-event terms. Death counts are null, which means they are not reported in the registry record, not that the record establishes zero deaths.

The registry does not describe how adverse events were collected, defined, graded, or assessed for relation to treatment. It also does not explain the difference between the safety at-risk counts and the primary outcome counts. With limited event counts and missing detail, the safety entries should be read as a brief registry report rather than a comprehensive comparative safety analysis.

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

The posted results describe averages from a randomized comparison of two active renin-angiotensin system inhibition regimens in people with type 2 diabetes and microalbuminuria. For the primary urinary albumin:creatinine ratio, the aggressive-inhibition arm had a higher posted mean than the low-dose arm, and the estimated mean difference was 120.1. The confidence interval is wide and includes zero, while the unadjusted p value is 0.592.

Those findings do not establish that aggressive inhibition produces a higher underlying mean, nor do they establish that the regimens have the same effect. The interval remains compatible with differences in either direction. A result that does not provide strong evidence against a zero difference is not equivalent to evidence that the difference is zero. Likewise, the direction of the observed means alone does not prove a causal effect or indicate how the result should be applied.

The trial record does not report a threshold for a clinically important change, an equivalence margin, or a formal non-inferiority objective. Without those criteria, the statistical estimates cannot determine whether a difference is meaningful in clinical terms. The listed secondary endpoints add measures of kidney function and vascular features, but their unadjusted results and undocumented multiplicity approach do not provide a definitive resolution.

The record also leaves important analytic details unspecified: the analysis population, handling of missing observations, repeated-measure methods, and any baseline adjustment. The numbers reported for enrollment, primary endpoint groups, and safety denominators are not explained in relation to one another. These uncertainties limit conclusions about the completeness and generalizability of the result.

In short, the registry reports an uncertain primary comparison and similarly uncertain secondary comparisons. It does not demonstrate superiority, equivalence, or the absence of an effect. It is a description of posted trial results, not individualized medical guidance or a substitute for a complete clinical and statistical report.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it pairs a randomized design with a primary outcome that shows substantial variability and an imprecise between-arm estimate. Randomization provides a basis for comparing assigned regimens, but it does not eliminate uncertainty, particularly when the endpoint groups are small and the outcome values are widely spread. The interval around the primary contrast makes that uncertainty visible.

The contrast between a point estimate and its interval is especially important. A single mean difference can seem definite when read without context; the broad interval shows that the estimate is compatible with a range of possible underlying differences. A p value alone cannot convey that range, and a non-significant result should not be translated into equality.

The study also illustrates why registry denominators and analysis populations need clear explanation. The record lists enrollment of 46, but the primary results and safety results use different arm counts. Without an account of participant flow and analysis eligibility, readers cannot determine why the counts differ or how representative the reported averages are of the randomized population.

Finally, the registry lists multiple outcomes but does not document a multiplicity plan or formal secondary analyses. This makes the secondary results useful as descriptive context, but less suited to confirmatory claims. The posted planning estimates also demonstrate how sample-size requirements depend on the effect selected for detection: planning around smaller effects requires more participants. Because those calculations are based on the observed effects rather than the trial’s documented original design, they are illustrations, not a reconstruction of the original design.

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 study was unmasked, and the record does not state whether outcome assessors were masked. The randomization method, allocation concealment, baseline characteristics, and participant flow are not reported. These omissions prevent assessment of baseline balance and of how the reported analysis groups arose.

The primary outcome has a wide spread within both arms, and its confidence interval is broad. The outcome group counts are 12 and 11, whereas enrollment is listed as 46. Safety at-risk counts are 14 and 13. The registry does not explain these differences, identify missing observations, or define the analysis population. No conclusion about attrition or the reasons for the denominators should be inferred.

The record does not report how measurements over months 3 to 36 were combined, how missing values were handled, or what statistical procedures generated the intervals and p values. It also does not report baseline adjustment, the original sample-size justification, an analysis plan, or a multiplicity approach. These gaps limit reproducibility and make it difficult to judge whether the posted summaries correspond to prespecified analyses.

The listed endpoint and secondary outcomes are summary measures over stated timeframes. The record does not provide individual-level data, outcome distributions, visit-level trajectories, or detailed adverse-event definitions. Safety counts are sparse, death counts are not reported, and no serious-event terms are listed. Together, these limitations mean the record supports cautious description of the posted results, but not a comprehensive assessment of treatment effects, safety, or applicability beyond the study population.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Low Dose Versus Aggressive Inhibition of the Renin-Angiotensin-Aldosterone (RAS) to Treat Microalbuminuria — NCT00907374.
• Registry record last updated 2012-03-30; status last verified 2012-03.
• Results first posted 2012-03-30.
• 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

NCT00907374, titled “Low Dose Versus Aggressive Inhibition of the Renin-Angiotensin-Aldosterone (RAS) to Treat Microalbuminuria,” is a completed, randomized, unmasked, parallel-group study sponsored by Charles Drew University of Medicine and Science. The listed enrollment is 46, and the phase is recorded as NA.

The study compared 10 mg benazepril orally daily with an aggressive regimen of 40-80 mg benazepril plus 25-100 mg losartan, both orally once or twice daily. The primary endpoint was mean urinary albumin:creatinine ratio during months 3 to 36. Its estimated mean difference was 120.1, with a 95% confidence interval from -319.5 to 559.7 and an unadjusted p value of 0.592.

The registry also posts results for estimated glomerular filtration rate, carotid artery intima thickness, and endothelial dysfunction. The registry record does not report a multiplicity plan, analysis population, missing-data methods, or the trial’s original sample-size justification.