Effects of Pioglitazone on Insulin and Glucose Metabolism in Women With Polycystic Ovary Syndrome (PCOS): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of Pioglitazone on Insulin and Glucose Metabolism in Women With Polycystic Ovary Syndrome (PCOS) (NCT00868140), a randomized na study. The primary outcome is AUC DCI-IPG (%/Min).

2. Clinical Question

The distinction between the study hypothesis and the posted outcome timing is important. The hypothesis concerns how chronic treatment might alter metabolism, whereas the primary endpoint description explicitly places the measurements before treatment. The registry record therefore does not establish from this endpoint whether DCI-IPG changed during treatment. It also does not report a post-treatment primary endpoint result or a treatment-period change estimate.

3. Trial Design

The study was recorded as randomized, single masked, and parallel, with pioglitazone and placebo arms. The registry lists the phase as NA and enrollment as 51. It records PCOS as the condition and Virginia Commonwealth University as the sponsor. The study start is listed as 2009-02, primary completion as 2011-06, and status as terminated. A reason for termination is not reported in the registry record.

The pioglitazone arm description specifies pills at 45mg twice per day for 6 months. The placebo arm is described as a matching pill taken twice per day for 6 months. The registry does not identify who was masked, describe how allocation was concealed, or give further details of the randomization procedure. Those aspects of conduct are not reported in the registry record.

The primary outcome is AUC DCI-IPG (%/Min), with a timeframe of Baseline. The description says that DCI-IPG measurements were taken from blood samples at 15 minute intervals during a 2 hour oral glucose tolerance test before treatment with pioglitazone or placebo. The primary arm summaries each include 16 participants. The secondary outcome listings name the Matsuda Index, and its posted summaries also include 16 participants in each arm. The record lists 6 outcome measures, but the available descriptions do not provide a complete account of all measures or their results.

Although the record has an enrollment of 51, the endpoint summaries do not account for all enrolled participants. Reasons for the difference, exclusions from particular analyses, and the analysis population definition are not reported in the registry record. The record also lists 0 reported analyses. Thus, details such as an intention-to-treat or per-protocol approach, treatment adherence, and the handling of missing observations cannot be established from the posted information.

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.

Population: A total of 32 obese (body mass index, BMI, greater than or equal to 30 kg/m2 PCOS women, between 18-40 years old, were studied during the equivalent of the follicular phase of the menstrual cycle, as documented by a serum progesterone of less than or equal to 2 ng/ml.

6. Primary Endpoint

The registry lists the primary outcome as AUC DCI-IPG (%/Min), measured over Baseline.

The primary endpoint is titled AUC DCI-IPG (%/Min). It represents the area under the curve for DCI-IPG measurements during an oral glucose tolerance test. According to the registry description, blood samples were taken at 15 minute intervals during the 2 hour test, and values were expressed as a percentage of bioactivity measured at time 0. Negative values were defined as a decrease relative to the time 0 measurement. The unit is listed as % bioactivity at time 0 of OGTT.

In general, an area under the curve combines measurements across a defined observation period into a measure of the overall pattern over that period. Such a summary can describe a response over the test more broadly than a single sample would. DCI-IPG is relevant to the stated biological hypothesis because the study rationale concerns insulin-stimulated release of this mediator and its possible relationship to DCI metabolism.

The key interpretive qualification is timing: the endpoint timeframe is Baseline, and the description says the test occurred before treatment. The posted values therefore summarize baseline measurements by randomized arm. They are not treatment-period changes, and they cannot establish whether either treatment altered the endpoint. Although the outcome title contains “AUC,” the registry describes its values as percentages of time-zero bioactivity; readers should use the listed unit and description when interpreting the scale.

7. Results Posted in the Registry

• 1/Pioglitazaone Treated: mean 13,162 versus 14,054 on control; difference -892.11 (95% CI -4,519 to 2,735), standardized effect d = -0.17; z-test p = 0.630.

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.

Matsuda 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 errors.
• Result:
  • 1/Pioglitazaone Treated: mean 3.36 versus 3.05 on control; difference 0.31 (95% CI -0.15 to 0.77), standardized effect d = 0.47; z-test p = 0.186.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1/Pioglitazaone Treated and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome listing names the Matsuda Index twice, and the posted results include one set of arm summaries and one comparison. That comparison is marked Baseline, like the primary endpoint. The overall pattern therefore consists of baseline summaries for both the primary and the posted secondary outcome, rather than a set of reported treatment-period changes across follow-up.

The Matsuda Index concerns insulin sensitivity, which is relevant to the proposed biological rationale for studying pioglitazone and DCI-IPG. But the relationship between an outcome’s scientific relevance and the evidence actually reported must be kept clear. A baseline comparison does not show that insulin sensitivity changed during treatment, nor does it establish that any change in insulin sensitivity led to a change in DCI-IPG. The record does not report an analysis linking changes in the two measures.

The posted secondary result is unadjusted. When multiple outcomes or comparisons are examined, the chance of finding an apparently unusual result somewhere among them can increase. A multiplicity plan can address how to interpret that family of tests, but such a plan is not reported in the registry record. For that reason, an unadjusted secondary p-value carries less weight as confirmatory evidence than a result interpreted under a prespecified and reported analysis strategy.

The registry lists 6 outcome measures, but the available secondary outcome entries and results do not give a complete picture of all measures or analyses. The record also lists 0 reported analyses. It is not possible to determine from this information which secondary questions were planned as confirmatory, how outcomes were selected for reporting, or whether any adjustments were applied beyond what is stated. The secondary results are best treated as limited descriptive and inferential information, with their baseline timing and unadjusted status kept in view.

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

• Matsuda Index
• Matsuda Index

9. Statistical Interpretation

10. Statistical Methods Explained

Continuous outcomes are commonly summarized by a mean and a measure of variability. Here, the primary and secondary outcome summaries report means with standard errors. A mean describes the center of the observed values in an arm. A standard error describes the estimated precision of that arm’s mean; it is not the same as the spread of individual participant measurements. The arm summaries list 16 participants for each posted endpoint.

What does the mean difference represent?

The reported mean difference compares the pioglitazone arm with the placebo arm. A negative estimate means the pioglitazone arm’s reported mean is lower than the placebo arm’s reported mean for that outcome; a positive estimate means it is higher. This direction is a description of the arithmetic comparison, not a statement about whether a difference is clinically important or caused by treatment. For the primary endpoint, the outcome is timed at baseline, so the mean difference is a baseline arm contrast.

A confidence interval gives a range of values compatible with the estimate under the assumptions of the analysis. Its width reflects precision: a wider interval leaves more uncertainty about the size and direction of the underlying difference. An interval that includes zero is compatible with no mean difference, but also with differences in either direction when the interval spans both. It should not be interpreted as proof that the arms are the same. The primary and secondary intervals are reported in the registry results.

How should a p-value be read?

A p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor the probability that the result happened “by chance.” The posted p-values are unadjusted. They do not convey the size or practical importance of a difference, and they do not compensate for a baseline endpoint or missing analysis details.

The registry identifies the outcome type as continuous and the summary parameter as a mean. It does not report the full statistical analysis plan, the precise model used for the reported comparisons, or whether covariate adjustment was planned or applied. The reported results can be described as mean differences with confidence intervals and unadjusted p-values, but details beyond those posted should not be inferred.

Why does timing matter to the comparison?

In a randomized treatment study, a treatment effect is usually assessed by comparing outcomes measured after treatment or by comparing changes from baseline, according to the prespecified analysis. Here, the primary endpoint timeframe is Baseline, and its description says measurements were taken before pioglitazone or placebo treatment. The summaries consequently do not measure a change caused by treatment. A difference at baseline can arise in the observed sample even when treatment has not yet begun; it is not an estimate of the effect of receiving treatment.

The registry’s secondary Matsuda Index outcome is also marked Baseline. Its comparison therefore has the same timing limitation. The record does not identify a reported follow-up comparison or change-from-baseline analysis for either outcome. Any treatment-effect interpretation would require evidence not present in the registry record.

Why can small samples make estimates uncertain?

With limited observations, a sample mean may be sensitive to the values of individual participants, and the interval around a group comparison may remain wide. That general statistical point helps explain why an estimate should be considered together with its confidence interval rather than read alone. It does not establish why the sample counts were as posted or whether the trial was designed to detect a particular effect. The original sample-size justification is not reported in the registry record.

The planning illustrations use a normal approximation and equal allocation, with a two-sided significance level of 0.05. They scale the effect to detect as a stated fraction of the observed effect. These are hypothetical planning calculations based on the posted effect estimate, not evidence of the trial’s original design or a report of what the trial could reliably detect. A smaller effect generally requires more participants to detect with the same target power under otherwise comparable assumptions.

What is not established by these methods?

The record does not report how missing measurements were handled, which participants were included in each analysis, or whether the analysis followed assigned treatment regardless of adherence. It does not report interim analyses or a multiplicity adjustment plan. The registry lists 0 reported analyses, and the outcome listings do not substitute for a full analysis plan. These absences matter because analysis choices can affect both the interpretation and the uncertainty of results, particularly when several outcomes or comparisons are considered.

General statistical concepts help readers understand the posted estimates, but they cannot fill in missing protocol details. The safest reading is to distinguish the numerical summaries that are reported from the analytic procedures and treatment-period results that are not reported in the registry record.

11. Confidence Intervals and Precision

The primary mean difference is -892.1, and its 95% confidence interval ranges from -4519.0 to 2735.0. This interval is broad and crosses zero. It includes values consistent with a lower primary mean in the pioglitazone arm as well as values consistent with a higher mean. The interval therefore leaves substantial uncertainty about the baseline difference’s direction and magnitude. It does not establish equivalence, and it is not a confidence interval for a treatment-period effect.

The reported arm means are 13160.0 for pioglitazone and 14050.0 for placebo. The standard errors are 1241.0 and 1373.0, respectively. Standard errors describe precision of the means rather than the range of individual participant values. The registry does not provide the individual observations or a separate description of their distribution, so the reported summaries cannot show how values varied within each arm.

For the Matsuda Index, the mean difference is 0.31, with a 95% confidence interval from -0.149 to 0.769. This interval also includes zero and permits differences in either direction. Its interpretation is likewise limited to the baseline comparison because the timeframe is listed as Baseline.

In general, confidence intervals communicate both an estimate and its uncertainty. Greater precision would correspond to a narrower interval, while a wider interval indicates that a broader range of values remains compatible with the data and analysis. The interval width should not be treated as a direct measure of clinical importance. Here, the baseline timing and lack of reported post-treatment comparisons are at least as important as the numerical precision when deciding what the results can answer.

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 illustrations are planning calculations, not counts of participants observed in the trial. The figures are participants per arm, rather than 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 a stated fraction of the observed effect. These assumptions describe the illustrations; the original sample-size assumptions for the trial are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a planning scenario designed to have an 80% chance of detecting the specified effect, if the assumptions used for the calculation hold and the specified effect is the true effect. The 90% power column expresses the corresponding planning target with a higher chance of detecting that effect, under those assumptions. Neither column is an observed result from the trial.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the planning calculation changes when the target effect is made smaller. For the primary endpoint, the corresponding figures range from 541 to 2,162 participants per arm for 80% power and from 724 to 2,894 participants per arm for 90% power. The displayed values should be read in their specific rows and columns rather than as one recommended trial size. Smaller effects need more participants to detect at a given power under otherwise similar assumptions, which is why the planning values rise as the assumed fraction falls.

The curve is another way to view the relationship between the target effect and the planning requirement; it does not add evidence about treatment response. These calculations are based on the observed estimate and are not observed power. They do not show that the trial’s original design used the same assumptions or that the posted baseline comparison was a treatment effect.

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 = -892.110; pooled standard deviation σ = 5234.113.
2. n = 2 × (1.96 + 0.842)² × 5234.113² / -892.110² = 540.4, rounded up to 541 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 <- -892.110000000001                      # observed difference in means
sigma <- 5234.11270035333                     # 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(868140)
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 = 541 (80% power), 724 (90% power)
 75% of observed effect: n per arm = 961 (80% power), 1,287 (90% power)
 50% of observed effect: n per arm = 2,162 (80% power), 2,894 (90% power)
power.t.test: 541.3 
Simulated power at n = 541 per arm: 0.796 (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

Multiplicity arises when a study evaluates more than one outcome, comparison, time point, or subgroup. If each test is interpreted separately without accounting for the full set of tests, the chance of at least one apparently noteworthy result can be higher than the chance associated with a single test. This general issue is relevant because the registry lists 6 outcome measures and the posted secondary outcome listings name the Matsuda Index twice.

The registry record does not report a multiplicity strategy, such as a hierarchy of outcomes, an adjustment procedure, or a rule for interpreting secondary analyses. The p-values posted for the comparisons are unadjusted. Without a stated plan, they should not be treated as if they were corrected for examining multiple outcomes. The record also lists 0 reported analyses, so it does not provide a complete analysis account from which to determine how the listed outcomes were handled.

Missing-data methods and analysis populations are also not reported. The overall enrollment is 51, but the primary and secondary arm summaries each include 16 participants per arm. The registry does not explain the difference, identify the number of participants with missing measurements, state whether participants were excluded, or describe imputation or other missing-data procedures. It does not say whether analyses used all randomized participants, only participants with observed endpoint measurements, or another population.

The record confirms randomized allocation but does not state whether the analysis followed assignment regardless of treatment adherence. It does not report adherence, crossovers, protocol deviations, or the handling of withdrawals. Those details are important to evaluating how an analysis reflects the randomized comparison. No interim analyses or stopping rules are reported, and the terminated status is not accompanied by a reason in the registry record.

These omissions do not prove that a particular method was or was not used. They mean that the posted material does not support conclusions about multiplicity control, missing-data assumptions, analysis populations, or the completeness of follow-up. Any such conclusion would require information beyond the registry record.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event summaries report 0 affected participants among 26 at risk in the pioglitazone group and 0 among 25 at risk in the placebo group. These figures describe what was posted for serious adverse events; they do not establish that no serious events occurred outside the reported collection or observation, or that the groups have identical safety profiles. The registry lists no serious adverse event terms.

Deaths are recorded as null for both groups, so death counts are not reported in the registry record. The record also lists 3 other adverse events among 26 at risk in the pioglitazone group and 0 among 25 at risk in the placebo group. Those are separate from the serious-event figures and should not be conflated with them. The registry information does not identify the nature, timing, severity, or relationship to treatment of those other events.

Adverse-event counts are descriptive. Without further details about event definitions, surveillance, duration of observation, and participant follow-up, they do not by themselves establish whether an event was caused by a study treatment. The available figures should be read as the event counts recorded in the registry, not as a complete safety assessment.

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

The posted results describe baseline endpoint measurements in randomized arms. They show the primary AUC DCI-IPG mean difference and its confidence interval, along with a baseline Matsuda Index comparison. The primary confidence interval spans zero and is wide; the unadjusted p-value is 0.63. These statistics quantify the reported baseline comparison, not a change after treatment.

The record’s scientific question concerns whether pioglitazone, by improving insulin sensitivity and reducing circulating insulin, affects DCI metabolism and insulin-stimulated DCI-IPG release. The endpoint description places the primary measurements before treatment. The posted results therefore do not answer whether pioglitazone altered DCI-IPG during the 6-month treatment period. Nor do they establish the proposed biological pathway or a link between changes in insulin sensitivity and DCI-IPG.

A non-significant p-value is not proof that there is no effect, and a confidence interval that includes zero is not proof that the arms are equivalent. Conversely, the numerical estimate alone is not evidence of a clinically meaningful effect. Precision, outcome timing, and the analysis population all matter. Here, the broad interval leaves uncertainty about the baseline difference, and the treatment-period effect is not reported in the registry record.

The record also does not explain why the trial was terminated, how the endpoint summaries came to include 16 participants per arm despite enrollment of 51, whether follow-up was complete, or how missing data and multiplicity were handled. Those gaps limit what can be concluded about completeness and analysis. They should not be filled by assuming a particular reason or method.

Accordingly, the result does not show that pioglitazone works or does not work for PCOS, and it does not establish benefit or harm. It documents the posted baseline comparisons and their statistical uncertainty. The central treatment question remains unanswered by the results described in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically notable because the stated biological hypothesis and the posted primary endpoint timing are not aligned for estimating a treatment effect. The rationale asks whether chronic reduction in circulating insulin could affect DCI metabolism and DCI-IPG release. Yet the primary endpoint is marked Baseline, and its description says measurements were taken before treatment. This makes careful attention to endpoint timing essential: a precise comparison at baseline would still not establish what treatment did afterward.

The record also illustrates why an estimate should be read together with its uncertainty. The primary mean difference is accompanied by a broad confidence interval that crosses zero. The point estimate alone cannot convey the range of values consistent with the analysis, and the unadjusted p-value cannot establish equivalence or rule out a treatment effect. At the same time, neither the interval nor the p-value answers the causal question when the endpoint is measured before treatment.

There is a second practical lesson in distinguishing enrollment from analysis counts. Enrollment is 51, but the posted summaries include 16 participants per arm. The record does not explain that difference. Without the analysis populations and missing-data account, readers cannot assess how the available summaries relate to the randomized participants as a whole.

Finally, the planning illustrations show how sample-size requirements depend on the effect chosen for planning, but they are not a retrospective verdict on trial quality or an account of the original design. Together, these features demonstrate the value of transparent outcome timing, analysis-population reporting, multiplicity plans, and complete results when interpreting a clinical trial.

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.

The central limitation for interpretation is that the primary outcome is recorded at baseline, before treatment. The reported comparison therefore does not estimate a treatment-period difference or change. The secondary Matsuda Index outcome is also listed at baseline, so it does not supply a reported treatment-period measure of insulin sensitivity.

The registry lists enrollment as 51, but the posted endpoint summaries include 16 participants in each arm. No explanation of the difference, participant flow, analysis population, or missing-data handling is reported. It is not possible to determine whether the posted summaries represent all randomized participants, a subset with measurements, or another defined group.

The record gives a terminated status but does not report the reason for termination. It also does not report the original sample-size justification, full statistical analysis plan, multiplicity approach, interim analyses, or stopping rules. Details of the single masking and allocation concealment are not reported. These omissions limit assessment of study conduct and analysis; they do not establish that any particular procedure was absent.

The primary estimate has a broad confidence interval, and the reported p-value is unadjusted. The registry lists 6 outcome measures but does not provide a complete account of all their results or analyses. The adverse-event record gives limited counts, with death counts not reported and little event detail. Finally, the results do not include a posted post-treatment primary outcome analysis. Together, these limitations constrain both the precision of interpretation and the ability to answer the trial’s stated treatment question.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effects of Pioglitazone on Insulin and Glucose Metabolism in Women With Polycystic Ovary Syndrome (PCOS) — NCT00868140.
• Registry record last updated 2016-06-10; status last verified 2016-05.
• Results first posted 2016-06-10.
• 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

This record describes a randomized, single-masked, parallel comparison of pioglitazone and placebo in obese women with PCOS. Enrollment is listed as 51, and the study status is terminated. Pioglitazone was described as 45mg twice per day for 6 months, with a matching placebo comparator.

The primary outcome is baseline AUC DCI-IPG during an oral glucose tolerance test. Its reported mean difference is -892.1, with a 95% confidence interval from -4519.0 to 2735.0 and an unadjusted p-value of 0.63. The secondary Matsuda Index result is also marked baseline. These results do not estimate treatment-related change. The record does not report a reason for termination, a complete analysis plan, or an explanation for the endpoint sample counts.