Effect of Ursolic Acid Administration on Insulin Sensitivity and Metabolic Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Ursolic Acid Administration on Insulin Sensitivity and Metabolic Syndrome (NCT02337933), a randomized phase 2 study. The primary outcome is Total Insulin Sensitivity.

2. Clinical Question

The trial addresses a metabolic measure rather than a clinical event such as a diagnosis or cardiovascular outcome. Its stated aim was to evaluate ursolic acid’s effect on insulin sensitivity and metabolic syndrome. The posted primary outcome is total insulin sensitivity at week 12, expressed as an index. Baseline measurement is mentioned in the outcome description, but a baseline result or a baseline-adjusted comparison is not reported in the registry record.

The registry also lists body weight, body mass index, total cholesterol, LDL cholesterol, creatinine and uric acid as secondary outcomes. The results available for interpretation include selected outcomes rather than a full account of all listed measures. The primary comparison therefore concerns the week 12 index; it does not by itself answer whether the intervention changed every component of metabolic syndrome, or whether any changes translated into fewer cases of diabetes or cardiovascular disease.

3. Trial Design

The registry identifies this as a phase 2, randomized, double-blind, parallel-group trial sponsored by the University of Guadalajara. Enrollment is recorded as 24. The outcome summaries report 12 participants in the ursolic-acid group and 12 in the placebo group. Randomization and double masking describe the intended allocation and masking features, but the methods used to generate the allocation sequence, conceal assignments, and maintain masking are not reported in the registry record.

The ursolic-acid group received 150 mg once a day before breakfast for 12 weeks. The placebo group received 150 mg of calcined magnesia capsules on the same daily schedule for 12 weeks. The registry lists the study status as completed, with a start recorded as 2014-09 and primary completion as 2015-09. These dates describe the study record and do not provide information about the timing of analysis or reporting.

The trial used a parallel design, meaning the registry describes separate groups receiving the assigned intervention rather than participants switching between treatments. The primary outcome was total insulin sensitivity at week 12. The outcome description says insulin sensitivity was calculated at baseline and week 12, but the reported group summaries concern the week 12 Matsuda index. Whether the primary analysis compared endpoint values, changes from baseline, or adjusted values is not reported in the registry record.

Further design details—including eligibility criteria, recruitment setting, the planned sample-size rationale, protocol deviations, analysis populations, missing-data handling and any interim analyses—are not reported in the registry record. Those omissions limit assessment of how closely the posted outcome summaries represent the original protocol and the randomized groups.

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.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Total Insulin Sensitivity, measured over Week 12.

The primary endpoint is total insulin sensitivity at week 12, measured using the Matsuda index. The registry describes calculating insulin sensitivity at baseline and week 12 and says the reported value corresponds to the week 12 index. It also notes that the Matsuda index is used to indicate insulin resistance. The outcome is reported as a mean with a standard deviation, in index units.

As general statistical context, a continuous index can summarize a physiological measure on a numeric scale, allowing group averages and their uncertainty to be compared. The Matsuda index was selected in this study to represent insulin sensitivity, which is central to the trial’s stated research question. A group difference in this measure is not the same as a difference in diabetes diagnoses, cardiovascular events, or all features of metabolic syndrome. No such clinical-event outcome is identified as the primary endpoint.

The registry gives week 12 means of 4.2 for ursolic acid and 2.6 for placebo, with standard deviations of 1.2 and 1.4, respectively. These summaries describe the observed endpoint values, not a change from baseline. The baseline values and a baseline-adjusted treatment estimate are not reported in the registry record, so the endpoint result alone cannot establish how much either group changed during the trial.

7. Results Posted in the Registry

• Ursolic Acid: mean 4.20 versus 2.60 on control; difference 1.60 (95% CI 0.56 to 2.64), standardized effect d = 1.23; z-test p = 0.003.

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.

Body Weight

• 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:
  • Ursolic Acid: mean 71.00 versus 81.00 on control; difference -10.00 (95% CI -20.52 to 0.52), standardized effect d = -0.76; z-test p = 0.063.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ursolic Acid and the control. The interval gives the range of effects that remain compatible with the data.

Body Mass Index

• 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:
  • Ursolic Acid: mean 24.90 versus 32.10 on control; difference -7.20 (95% CI -9.51 to -4.89), standardized effect d = -2.50; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Ursolic Acid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Total Cholesterol

• 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:
  • Ursolic Acid: mean 5.20 versus 6.40 on control; difference -1.20 (95% CI -2.47 to 0.07), standardized effect d = -0.76; z-test p = 0.064.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ursolic Acid and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies six secondary outcomes as posted: body weight, body mass index, total cholesterol, LDL cholesterol, creatinine and uric acid. Detailed results are available for only selected secondary measures in the record summarized by these statistics. Taken together, the available results do not present a uniformly consistent pattern across metabolic measures. This broader pattern should be considered alongside the primary index result rather than treated as independent confirmation of it.

The registry reports Wilcoxon (Mann-Whitney) p-values for the secondary analyses, while the accompanying recalculations compare posted means. These approaches do not necessarily produce the same p-value because they test different features of the data. In the secondary results, the reported tests and the mean-based recalculations are not uniformly aligned. That difference cautions against interpreting any one secondary p-value in isolation; the rank-based result should not be read as if it were a test of the recalculated mean difference.

General statistical context: when many outcomes are examined, some may appear notable by chance even if no underlying effect exists. The registry lists 13 outcome measures and 13 analyses, but a multiplicity-adjustment plan is not reported in the registry record. Unadjusted secondary p-values therefore carry less weight than a prespecified primary comparison, particularly when the selection and analysis of outcomes are not fully described.

Secondary outcomes can help characterize whether a primary finding sits alongside changes in related measures, but they do not independently establish an effect on the primary endpoint. Nor do the listed measures cover every component of metabolic syndrome or clinical outcomes such as diabetes or cardiovascular disease. Interpretation is limited by the subset of results posted, the lack of a reported adjustment strategy, and the absence of a stated hierarchy or confirmatory role for the secondary outcomes.

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

• Body Weight
• Body Mass Index
• Total Cholesterol
• Low Density Lipoproteins Cholesterol (LDL-c)
• Creatinine
• Uric Acid

9. Statistical Interpretation

10. Statistical Methods Explained

What the reported summaries describe. The registry reports a mean and standard deviation for the week 12 primary outcome in each group. A mean describes the group’s average index value; the standard deviation describes the spread of values around that average. These are descriptive summaries. They do not show the distribution of individual values, whether the distribution was symmetric, or whether any participants had unusually influential observations.

What the recalculated comparison means. The unadjusted recalculation compares the posted group means. It estimates the mean difference as ursolic acid minus placebo: 1.6 index units. “Unadjusted” means the calculation uses the posted summary values without adjustment for baseline measures or other covariates. It is a separate summary-statistic calculation, not a reconstruction of participant-level data or a substitute for the sponsor’s analysis.

Why two test approaches can appear. The registry reports a Wilcoxon (Mann-Whitney) test for the primary comparison. This is a rank-based method that compares the ordering of observations between groups; it is not a test specifically of the difference between arithmetic means. The recalculated comparison uses the reported means and standard deviations to assess a mean difference. Similar p-values do not make the methods equivalent: the estimands and assumptions differ. General statistical context: rank-based tests can be useful when a comparison based on ranks is desired, while a mean-based estimate directly describes a difference in averages. The registry does not report why the Wilcoxon method was chosen, whether its assumptions were checked, or a fuller analysis plan.

How to read a p-value. A p-value describes how unusual data at least as incompatible with a null comparison would be under that null model and the test’s assumptions. The reported primary p-value is 0.003. It is not the probability that treatment has no effect, and it does not quantify the size of a difference. Effect size and uncertainty are better considered using the estimated difference and its confidence interval alongside the outcome scale and study context. The registry does not report a threshold defining a clinically important index difference.

Why uncertainty matters. A confidence interval gives a range of estimates compatible with the observed data under the calculation’s assumptions. A narrower interval indicates greater statistical precision for that particular estimate; a wider interval indicates less precision. General statistical context: an interval does not account for every potential bias, such as missing outcome data, selective reporting, or problems in allocation or masking. Nor does it guarantee that the true effect lies within the displayed range.

What the standard deviations add. The standard deviations are 1.2 in the ursolic-acid group and 1.4 in the placebo group. They provide information about observed variability within groups, while the confidence interval concerns uncertainty in the between-group estimate. These quantities answer different questions. Neither the group means nor the standard deviations reveal the full distribution of participant-level values, and participant-level data are not reported in the registry record.

Endpoint value versus change. The outcome description says values were calculated at baseline and week 12, but only the week 12 group summaries are posted for the primary endpoint. A comparison of endpoint means can differ from a comparison of changes, especially if baseline values differ. Because baseline summaries and the exact primary analysis model are not reported in the registry record, the recalculation should be understood strictly as an unadjusted comparison of the posted week 12 summaries.

Small samples and variability. General statistical context: with fewer observations, each participant’s value can have greater influence on a group summary, and estimates may have substantial uncertainty. This is a reason to examine intervals and methods, not a reason to dismiss a result automatically. The registry reports 12 participants per group for the primary outcome, but does not report diagnostics, sensitivity analyses, or how missing observations were handled. Those details would help assess robustness.

Association is not a complete clinical conclusion. The primary endpoint is a surrogate physiological index rather than a clinical event. A statistically detectable group comparison on this measure does not by itself establish what the result means for symptoms, diabetes, cardiovascular disease, or long-term health. General statistical interpretation requires distinguishing the endpoint actually measured from broader outcomes that were not reported.

11. Confidence Intervals and Precision

The recalculated mean difference in the week 12 Matsuda index is 1.6 index units, with a confidence interval of approximately 0.557 to 2.643. The interval lies above zero, which is consistent with a positive difference in the direction of the posted group means under this unadjusted calculation. Its width also signals that the estimate is not exact: values across a range remain compatible with the summary data and calculation assumptions.

The interval is calculated from the posted means and standard deviations and is not the interval from the registry’s Wilcoxon analysis. The registry does not report a confidence interval for its rank-based test. The interval therefore answers a mean-comparison question and should not be attributed to the sponsor’s test. It also does not account for uncertainty arising from missing data, unreported analytic choices, or selective outcome reporting.

Precision is not the same as importance. The interval concerns plausible values for the mean difference under the recalculation; it does not indicate whether any particular value is clinically meaningful. The registry record does not provide a threshold for a meaningful change in the Matsuda index. It also reports no baseline group summaries, so the interval does not describe a baseline-adjusted change.

Because the reported groups are small, further data could change both the estimated difference and its uncertainty. General statistical context: confidence intervals are most informative when read together with the study design, analysis method, measurement scale and risk of bias. The primary interval supports a positive difference in the posted week 12 means, while leaving questions about reproducibility, clinical interpretation and longer-term outcomes unresolved.

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 primary effect, not the trial’s original design assumptions. For this continuous outcome, the figures are participants per arm, not a total number of events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size justification is not reported in the registry record.

For planning around 100% of the observed effect, the illustration gives 11 participants per arm for 80% power and 14 participants per arm for 90% power. For planning around 75% of the observed effect, it gives 19 participants per arm for 80% power and 25 participants per arm for 90% power. For planning around 50% of the observed effect, it gives 42 participants per arm for 80% power and 56 participants per arm for 90% power.

In plain terms, the 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true one. The 90% column describes the corresponding planning target for a 90% chance. These are prospective planning concepts, not probabilities that the completed trial’s result is correct. This is not observed power.

The pattern illustrates a general principle: smaller effects are harder to distinguish from random variation, so planning for smaller effects requires more participants. These calculations use the observed effect as their starting point, and the observed estimate from a small trial may not be a stable estimate of the effect a future study should expect. The figures are therefore illustrations of how assumptions affect planning, not evidence that the trial was adequately or inadequately sized under its original plan.

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 = 1.600; pooled standard deviation σ = 1.304.
2. n = 2 × (1.96 + 0.842)² × 1.304² / 1.600² = 10.4, rounded up to 11 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 <- 1.6                      # observed difference in means
sigma <- 1.30384048104053                     # 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(2337933)
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 = 11 (80% power), 14 (90% power)
 75% of observed effect: n per arm = 19 (80% power), 25 (90% power)
 50% of observed effect: n per arm = 42 (80% power), 56 (90% power)
power.t.test: 11.5 
Simulated power at n = 11 per arm: 0.779 (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. Analyses Reported by the Sponsor

For the primary outcome, the registry reports a Wilcoxon (Mann-Whitney) analysis with p = 0.003. The unadjusted recalculation from the posted means and standard deviations estimates a mean difference of 1.6 index units and also gives p = 0.003. The numerical agreement in p-values does not mean the analyses are identical: the registry’s rank-based test and the recalculated comparison of means address the data in different ways.

The registry does not provide a sponsor-reported mean difference or confidence interval for the primary outcome. The recalculated estimate and interval are consequently useful as an unadjusted description based on the posted summary statistics, not as a replacement for the sponsor’s analysis or a participant-level reanalysis. The discrepancy indicator is false for the primary comparison; there is no flagged disagreement requiring one result to take precedence. Interpretation should nonetheless keep the methods distinct and recognize that the registry does not report the full analysis plan, baseline-adjusted results, or participant-level data.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple outcome measures, including several secondary metabolic outcomes. It does not report whether the protocol specified a multiplicity-control strategy, a hierarchy among secondary outcomes, or which secondary analyses were intended to be confirmatory. The number of outcome measures and analyses recorded does not, by itself, establish how the investigators planned to control the chance of false-positive findings.

General statistical context: testing several outcomes can increase the chance that at least one result appears statistically notable by chance. Adjustment methods or a prespecified testing hierarchy can address this issue, but they may change how results should be interpreted. Since such a plan is not reported in the registry record, secondary p-values should be treated as exploratory evidence rather than as a set of independent confirmations.

The registry reports the primary endpoint at week 12 and mentions calculations at baseline and week 12, but does not report a baseline-adjusted analysis, a change-score analysis, or the exact primary model. It also does not report an interim-analysis plan, stopping rules, sensitivity analyses, or a statistical-analysis plan. These absences mean the analytical choices and their relation to any prespecified protocol cannot be evaluated from the record.

Missing-data handling and analysis populations are also not reported in the registry record. The group summaries list 12 participants per arm, but the record does not state whether these figures represent all randomized participants, participants with observed endpoint data, or a particular analysis population. Attrition, exclusions after randomization, imputation, and reasons for missing outcomes are not described. Without those details, it is not possible to assess whether missingness could have affected the estimates or whether the posted analysis follows an intention-to-treat principle.

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 non-serious adverse event terms

For serious adverse events, the registry reports zero affected participants among 12 at risk in the ursolic-acid group and zero among 12 at risk in the placebo group. It also reports zero deaths in each group. These are counts recorded for the trial; they do not establish that serious events could not occur, particularly given the limited size and 12-week treatment period.

The record reports other adverse events affecting 4 participants in the ursolic-acid group and 6 in the placebo group. The event terms and further detail for these other events are not reported in the registry record. Counts alone do not describe event severity beyond the serious/non-serious categorization, timing, duration, recurrence, or whether investigators considered an event related to treatment.

These safety figures should be read as descriptive observations during the reported study, not as a precise comparison of risk. The record does not provide a detailed safety analysis, confidence intervals, or information about follow-up after treatment. The absence of reported serious events in these groups is not evidence that uncommon or later events are ruled out.

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

The primary result describes a difference in the week 12 Matsuda index between the randomized groups. The ursolic-acid group had a mean of 4.2 and the placebo group had a mean of 2.6. The unadjusted recalculation estimates a mean difference of 1.6 index units, and the sponsor’s reported primary test has p = 0.003. Within the limits of the registry record, the posted data support a between-group difference on this measured index at the stated time point.

The finding does not establish that ursolic acid prevents or treats diabetes, cardiovascular disease, or metabolic syndrome as a whole. Those clinical outcomes are not reported as primary results. The Matsuda index is a physiological measure, and the record supplies no threshold for interpreting a difference as clinically important. It also does not provide a longer-term assessment, so persistence of the week 12 comparison is unknown.

The result does not show the amount of change from baseline because baseline group values are not reported. It is not possible to determine from the posted summary whether the endpoint contrast would be different after baseline adjustment. Nor does a statistically notable p-value tell the probability that the result is true, its clinical importance, or how likely the finding is to recur in another study.

The trial’s sample size and incomplete reporting of analysis details call for caution. The available results do not resolve questions about missing data, outcome multiplicity, participant characteristics, or generalizability to people outside the enrolled population. The most defensible interpretation is therefore narrow: a short-term group difference was reported for the primary index, with uncertainty and important limits on what can be inferred about broader health outcomes.

18. Why This Trial Matters Statistically

This trial offers a useful example of why an endpoint, an analysis method and an effect estimate should be distinguished. The primary outcome is a continuous index, the sponsor’s reported test is rank-based, and the accompanying recalculation estimates a difference in group means. Although the primary p-values match numerically, the methods do not answer exactly the same statistical question. Reading the estimate and its uncertainty alongside the reported test makes that distinction visible.

The record also illustrates how a small study can yield a result that appears statistically notable while leaving uncertainty about magnitude, reproducibility and clinical importance. A p-value does not replace an effect estimate or confidence interval, and a confidence interval does not resolve bias or incomplete reporting. The index difference is not interchangeable with evidence about clinical events or long-term outcomes.

Several design and reporting details matter for interpretation: baseline endpoint values, missing-data methods, analysis populations, a multiplicity plan, and the rationale for the original sample size are not reported in the registry record. These details are not peripheral; they help determine what comparison was planned, how robust it may be, and how much confidence to place in secondary findings.

Finally, planning illustrations based on the observed effect demonstrate why sample-size calculations depend on the effect a future study aims to detect. They should not be mistaken for evidence about the power of the completed trial. Together, these issues make the study statistically instructive as a case in separating observed results from broader conclusions.

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.

The trial’s reported enrollment is 24, and the primary outcome summaries list 12 participants in each group. Estimates from a small study can be sensitive to individual observations, and the record does not provide participant-level data or sensitivity analyses that would help assess robustness. The enrollment figure alone does not clarify whether all randomized participants contributed primary-outcome data.

The primary result is reported at week 12, while baseline outcome values are not reported. The registry says insulin sensitivity was calculated at baseline and week 12 but does not specify the exact primary analysis model or whether the posted comparison was adjusted for baseline. This limits interpretation of the endpoint means as evidence of change during treatment.

Important population details—including eligibility criteria, participant characteristics and recruitment setting—are not reported in the registry record. This restricts assessment of how representative the participants were and how broadly the result might apply. The record also does not describe adherence, treatment discontinuation, protocol deviations, allocation concealment, or how masking was implemented.

The statistical-analysis plan, missing-data approach, analysis populations, original sample-size rationale, interim analyses, and multiplicity strategy are not reported. The record lists more outcome measures than the selected secondary results described in detail, which limits a complete assessment of secondary patterns and selective reporting. Follow-up beyond the stated treatment period is not described, and the primary endpoint is an index rather than a clinical outcome. These limitations constrain conclusions about durability, broader metabolic effects, and health outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Ursolic Acid Administration on Insulin Sensitivity and Metabolic Syndrome — NCT02337933.
• Registry record last updated 2020-10-08; status last verified 2020-09.
• Results first posted 2020-10-08.
• 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

The registry describes a completed, randomized, double-blind, parallel phase 2 trial sponsored by the University of Guadalajara. It enrolled 24 participants and compared ursolic acid, 150 mg once a day before breakfast for 12 weeks, with placebo capsules containing calcined magnesia on the same schedule.

The primary outcome was the week 12 Matsuda index. Reported means were 4.2 for ursolic acid and 2.6 for placebo; the sponsor reports a Wilcoxon (Mann-Whitney) p-value of 0.003. An unadjusted recalculation estimates a mean difference of 1.6 index units, with an interval approximately 0.557 to 2.643. The record also reports selected secondary outcomes and adverse-event counts.

Baseline values, the original sample-size rationale, missing-data methods, analysis populations, and a multiplicity plan are not reported in the registry record. The result is a short-term comparison on an insulin-sensitivity index and does not, by itself, establish effects on clinical outcomes or longer-term health.