Use of Rosuvastatin in HIV-Infected Subjects to Modulate Cardiovascular Risks: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Use of Rosuvastatin in HIV-Infected Subjects to Modulate Cardiovascular Risks (NCT01218802), a randomized phase 2 study. The primary outcome is Bone Mineral Density (BMD).

2. Clinical Question

The registry’s broader hypothesis concerned whether 96 weeks of rosuvastatin would be safe and effective in decreasing cardiovascular risk and bone loss in the HIV-positive population. The posted primary outcome addressed bone mineral density, not every part of that broader hypothesis. The result therefore describes this specific bone measure and time point; it is not a complete assessment of cardiovascular risk or all aspects of bone health.

The registry reports the outcome as a continuous measure summarized by means and standard deviations. The comparison is the mean difference between the rosuvastatin and placebo groups. This asks whether the average percentage change differed between the groups; it does not describe how every participant’s measurement changed or establish the cause of an individual change.

3. Trial Design

This was a randomized, phase 2, placebo-controlled trial with a parallel-group model and triple masking. The registry lists 147 enrolled participants and identifies University Hospitals Cleveland Medical Center as the sponsor. The recorded study start was 2011-02, primary completion was 2014-05, and the status is completed.

Participants were assigned to rosuvastatin or a sugar-pill placebo. The active regimen was rosuvastatin 10 mg daily for 96 weeks. The placebo was described as externally similar to the active drug and taken as one capsule daily. Randomization is intended to allocate participants to groups by chance, while masking is intended to limit the influence of treatment knowledge on participants or study personnel. The registry labels masking as triple but does not identify the masked roles in the record details used for this outcome.

The primary outcome was bone mineral density, expressed as percentage of change and measured by change in bone DEXA from baseline to week 96. The posted outcome data include 59.0 participants in the rosuvastatin group and 55.0 in the placebo group. The registry notes that the number with valid outcome data was less than total enrollment because of dropouts before week 96 and/or invalid DEXA testing data.

The record lists two outcome measures, but no secondary outcomes are posted in the results information. It reports no analyses in its analysis listing. Further details of the original sample-size justification, statistical analysis plan, allocation procedure, and masking roles are not reported in the registry record. Those omissions limit how much can be inferred about the planned analysis beyond the design features explicitly recorded.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The total number of participants who received this outcome who had valid data is less than the total number of enrolled participants, due to drop outs before week 96 and/or invalid testing data from DEXA results.

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 Bone Mineral Density (BMD), measured over 96 weeks.

The primary endpoint is bone mineral density (BMD), reported as percentage of change over 96 weeks. It was measured by comparing bone DEXA results at baseline with results at week 96. The registry describes the outcome statistic as a mean and its spread as a standard deviation.

As a general measurement concept, a continuous endpoint retains the magnitude of a measured value rather than reducing it to categories such as improved or not improved. A group mean describes the average change, while the standard deviation describes the spread of participant measurements around that average. These summaries address different features of the data: the mean captures the group’s central tendency, and the standard deviation indicates how variable the measurements were.

BMD is relevant to this trial because the registry’s stated hypothesis included decreasing bone loss. DEXA provides the measurement used for this endpoint. The outcome is specific: it concerns change in BMD between baseline and week 96. It does not, by itself, measure cardiovascular outcomes, all bone-related outcomes, or changes at other times. Nor does a group mean indicate that participants had identical responses.

The valid-data group sizes are smaller than the total enrollment. The registry attributes this to dropout before week 96 and/or invalid DEXA testing data, without giving the number attributable to each reason or describing how missing measurements were handled. Thus, the endpoint summaries describe participants with valid data for this measure, rather than necessarily all enrolled participants.

7. Results Posted in the Registry

• Rosuvastatin: mean -0.03 versus -0.53 on control; difference 0.50 (95% CI -0.45 to 1.45), standardized effect d = 0.19; z-test p = 0.302.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the mean difference represent?

For a continuous endpoint, a group mean is the arithmetic average of the measured values in that group. The reported comparison is a mean difference: the rosuvastatin group’s mean change minus the placebo group’s mean change. Its estimate is 0.5, on the endpoint’s scale of percentage of change. A positive estimate means the rosuvastatin group mean is higher on that scale than the placebo mean. This direction describes the coding of the comparison and does not, by itself, establish importance or certainty.

The group summaries show means of -0.03 and -0.53, with standard deviations of 2.45 and 2.7. A standard deviation describes how dispersed individual values are around a group mean. It is not the standard error of the mean and is not a confidence interval. The standard error instead describes the sampling uncertainty of an estimate, such as a group mean or between-group difference. The registry does not post a separate standard error for the mean difference in the available comparison information.

How should the confidence interval be read?

A confidence interval expresses the statistical uncertainty around an estimate under the method used to construct it. The posted interval for the mean difference is -0.449 to 1.449. Because the interval includes zero, values consistent with no difference are included, as are values on either side of zero. The interval is not a range containing a known proportion of individual participants’ changes, and it does not assign a probability to the true effect after the data have been observed.

Confidence intervals are useful because a point estimate alone can make an uncertain comparison look more exact than it is. In this case, the point estimate is 0.5, while the interval covers a range that includes both negative and positive differences. The interval therefore cautions against treating the observed direction of the point estimate as conclusive. Its interpretation depends on the statistical method and assumptions, details of which are not fully reported in the registry record.

What does the p-value add?

The posted unadjusted p-value is 0.302. In general, a p-value describes how compatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, the probability that chance alone caused the result, or a measure of the size or clinical importance of an effect. A p-value also does not convey the full range of estimates compatible with the data; the confidence interval is useful for that purpose.

The word unadjusted matters because the record does not describe an adjustment for testing multiple outcomes or comparisons. The p-value should be read as the posted unadjusted statistic, rather than as evidence that multiplicity was addressed. The statistical analysis plan and any prespecified decision threshold for this outcome are not reported in the registry record. The sample-size planning illustration refers to a two-sided significance level of 0.05, but that illustration is not evidence of the trial’s original analysis plan.

Why does variability matter?

Continuous measurements can vary among participants even when they belong to the same treatment group. Standard deviations of 2.45 and 2.7 indicate that individual measurements were dispersed around their respective group means. General statistical reasoning explains why this matters: greater variation makes it harder to estimate a group average precisely, unless there is enough information to offset that variation. The observed standard deviations are descriptive, while the confidence interval captures uncertainty in the between-group estimate under its calculation method.

Over-dispersion is a general concern when observed variability is greater than a model assumes. If a method assumes too little variability, its uncertainty estimates can be too small and its intervals too narrow. The registry does not report an over-dispersion assessment for this continuous endpoint, and the available summaries do not justify claiming that over-dispersion occurred. This concept is relevant as a general reminder that the reliability of an interval depends on how well the analysis assumptions fit the data.

What can be said about analysis populations?

The posted outcome data include 59.0 rosuvastatin participants and 55.0 placebo participants. The registry says valid data were available for fewer people than were enrolled because of dropout before week 96 and/or invalid DEXA results. It does not report the exact number excluded for each reason, the number with any partial data, or an imputation method. Nor does it identify whether the results come from an intention-to-treat, per-protocol, or another named analysis population. Those details should not be inferred from the outcome counts alone.

The record lists no analyses in its analysis listing, even though it posts the outcome summaries and comparison statistics. This means the available record does not provide a fuller account of model specification, covariate adjustment, diagnostic checks, or prespecified analysis choices. The comparison can be described from the posted estimate, interval, and p-value, but unreported methodological details remain unknown.

How does the design relate to the analysis?

Randomization, placebo control, parallel groups, and triple masking are listed design features. In general, random assignment is intended to support a fair comparison by reducing systematic differences in treatment assignment; masking can reduce some influences of treatment awareness. These design features do not remove uncertainty due to finite data, missing outcome measurements, or limitations in reporting. The registry does not describe the randomization procedure, the masked roles, or methods used to preserve allocation concealment. Statistical interpretation should distinguish the design labels from implementation details that are not reported.

10. Confidence Intervals and Precision

The principal estimate is a mean difference of 0.5, with a confidence interval from -0.449 to 1.449. Precision concerns how narrowly the data locate an estimate. A narrower interval generally indicates less statistical uncertainty under the method used; a wider interval indicates that a broader range of effects remains compatible with the data. The interval crosses zero, so the result does not resolve whether the underlying mean difference is negative, zero, or positive.

The interval should not be read as showing that the true difference must lie within its endpoints. In general, a confidence interval is a procedure with a stated long-run coverage property when its assumptions hold. It is not a guarantee for an individual study, and it does not describe the spread of participant outcomes. The standard deviations of 2.45 and 2.7 describe within-group variability; the confidence interval describes uncertainty about the between-group mean difference.

There were 59.0 participants with valid BMD data in the rosuvastatin group and 55.0 in the placebo group. The registry notes that valid outcome data were unavailable for some enrolled participants due to dropout before week 96 and/or invalid DEXA testing. Missing data can affect precision and may also affect the estimated comparison if the people with valid measurements differ systematically from those without them. The record does not report enough detail to evaluate that possibility or the method used to address missingness.

The unadjusted p-value of 0.302 is another summary of evidence under a statistical model, but it does not make the estimate more precise than the confidence interval indicates. No adjusted interval or analysis addressing other outcomes is reported in the registry record. The available precision assessment is therefore limited to the posted unadjusted comparison and its interval.

11. 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 figures are participants per arm, not total events. They are illustrations based on the observed effect, rather than the trial’s own original design assumptions. The stated 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 a stated fraction of the observed effect. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the displayed figures are 416 participants per arm for 80% power and 557 participants per arm for 90% power. For planning at 75% of the observed effect, they are 740 participants per arm for 80% power and 990 participants per arm for 90% power. For planning at 50% of the observed effect, they are 1,664 participants per arm for 80% power and 2,227 participants per arm for 90% power.

In plain language, the 80% power column gives the estimated number of participants per group for a future study to have an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the assumptions are correct. The 90% column describes the corresponding planning target for a higher chance of detection. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm in these illustrations.

These figures are not observed power. They are prospective planning illustrations calculated using the observed effect as their reference, and should not be read as a statement about the probability that the completed trial detected an effect.

12. 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 = 0.500; pooled standard deviation σ = 2.574.
2. n = 2 × (1.96 + 0.842)² × 2.574² / 0.500² = 415.9, rounded up to 416 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 <- 0.5                      # observed difference in means
sigma <- 2.57356929741001                     # 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(1218802)
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 = 416 (80% power), 557 (90% power)
 75% of observed effect: n per arm = 740 (80% power), 990 (90% power)
 50% of observed effect: n per arm = 1,664 (80% power), 2,227 (90% power)
power.t.test: 416.8 
Simulated power at n = 416 per arm: 0.800 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists two outcome measures, but no secondary outcomes are posted in the results information. It reports no analyses in its analysis listing. The available record does not describe a multiplicity adjustment, a hierarchy of outcomes, or a prespecified primary testing strategy beyond identifying BMD as the primary outcome. The p-value posted for the comparison is unadjusted. It is therefore not possible to determine from the record whether the reported analysis was one of several comparisons considered or how any other analyses were handled.

Multiplicity is a general statistical issue that arises when several outcomes, time points, subgroups, or comparisons are tested. As the number of tests increases, the chance of at least one apparently unusual result can also increase under a null model. Adjustment procedures or a prespecified testing strategy can address this issue, but the registry record does not report whether either was used. No adjustment should be assumed.

Missing outcome data are explicitly noted. The number with valid data was less than total enrollment because of dropouts before week 96 and/or invalid DEXA testing. The registry does not quantify these reasons separately, report whether data were missing for other reasons, or describe an imputation or sensitivity analysis. It also does not report whether missingness was considered related to treatment assignment or observed outcomes. As a general matter, missingness can reduce precision, and systematic differences between participants with and without measurements can affect the comparison.

The record does not name the analysis population used for the BMD comparison. It does not say whether all randomized participants were analyzed as assigned, whether the analysis was limited to participants completing the outcome assessment, or whether another population definition was used. The outcome counts alone do not establish a specific analysis approach. Consequently, the posted result is best described as based on the participants with valid outcome data, with the handling of other enrolled participants not reported in the registry record.

Details of the statistical analysis plan, adjustment for baseline values, covariate selection, interim analyses, and the original sample-size justification are not reported in the registry record. Their absence prevents a detailed assessment of prespecification and analysis choices, but it does not justify guessing what methods were used.

14. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: elevated creatinine kinase (1.4%).

The registry reports serious adverse events for 72 participants at risk in the rosuvastatin group, with 1 affected, and for 75 participants at risk in the placebo group, with 0 affected. For other adverse events, it reports 5 affected among 72 at risk in the rosuvastatin group and 5 among 75 at risk in the placebo group. These are descriptive counts, separate from the BMD endpoint comparison.

The top listed serious adverse-event term is Elevated Creatinine Kinase, reported as 1.4%. The record does not provide further event-level detail in the information available for these results, such as timing, severity grading, relatedness assessments, or the number of events per affected participant. The registry’s death entries are not reported in the registry record; they should not be interpreted as zero deaths.

These counts should be read with their listed at-risk denominators and with the limits of the record in mind. They do not by themselves establish a comparative safety profile or explain whether events were caused by treatment. The registry information cited does not describe exposure-adjusted rates or the criteria used to classify adverse events.

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

The posted BMD means show a percentage change of -0.03 in the rosuvastatin group and -0.53 in the placebo group at 96 weeks. The estimated mean difference was 0.5, with a confidence interval from -0.449 to 1.449 and an unadjusted p-value of 0.302. The interval includes zero and values in both directions, so the estimate does not precisely settle the direction of the underlying group difference.

This result does not show that the groups were equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether effects fall within that margin; such a margin or analysis is not reported in the registry record. Nor does the result prove that there was no difference. Rather, the posted estimate has uncertainty, and the data summarized in the record do not rule out a range of possible mean differences.

The result also does not establish the effect of rosuvastatin on cardiovascular risk, despite the broader hypothesis in the study summary. The primary endpoint is BMD measured by DEXA from baseline to week 96. No cardiovascular outcome estimate is included in the posted results. Likewise, a mean change in BMD is not a complete description of bone health or of individual participants’ experiences.

The analysis is limited by the fact that valid BMD results were available for fewer participants than were enrolled. The registry attributes this to dropout before week 96 and/or invalid DEXA testing, but does not report the exact pattern or its analytic treatment. The reported adverse-event counts add descriptive safety information but do not resolve the endpoint’s statistical uncertainty or establish causation.

Overall, the record documents a randomized, placebo-controlled comparison and posts an estimated mean difference with an interval and unadjusted p-value. Those statistics support a cautious description of the observed data, not a categorical claim that treatment did or did not change BMD.

16. Why This Trial Matters Statistically

This trial illustrates the distinction between the direction of a point estimate and the strength of evidence about an underlying effect. The observed mean difference was positive, but its confidence interval crossed zero and the unadjusted p-value was 0.302. Readers can therefore see both the direction suggested by the point estimate and the uncertainty that remains around it, rather than relying on the point estimate alone.

It also shows why continuous outcomes are often reported with both a mean and a measure of variability. The means describe average percentage change, while standard deviations of 2.45 and 2.7 describe the spread of participant results. A group average does not imply that participants had similar changes. Keeping these summaries distinct helps prevent a mean from being treated as a complete account of individual outcomes.

The record makes missing outcome data visible: fewer participants had valid BMD data than were enrolled, with dropout before week 96 and/or invalid DEXA testing identified as reasons. Yet it does not provide enough detail to assess the missing-data mechanism or analysis population. This is statistically important because incomplete measurement can influence both precision and interpretation.

Finally, the sample-size illustrations demonstrate how planning depends on the effect a study aims to detect. Under the stated assumptions, the listed participant targets grow as the planning effect becomes smaller. These are prospective planning calculations based on the observed effect, not evidence about the completed study’s chance of success. Together, the estimate, uncertainty, missing-data note, and planning assumptions show why registry results should be read as a combination of what is quantified and what remains unreported.

17. 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 outcome population is smaller than the total enrollment: valid BMD data were reported for 59.0 rosuvastatin participants and 55.0 placebo participants, compared with 147 enrolled overall. The registry attributes the reduced number to dropout before week 96 and/or invalid DEXA testing but does not separate those causes or report the complete pattern of missingness. The method used to handle missing measurements is not reported in the registry record.

The posted comparison is unadjusted. The record does not report a covariate-adjusted estimate, a baseline-adjusted analysis, or sensitivity analyses. It also does not identify a named analysis population or provide enough information to determine whether all randomized participants were included in the analysis. The posted valid-data counts should not be treated as proof of a particular analysis strategy.

The outcome is limited to mean percentage change in BMD measured by DEXA from baseline to week 96. The registry’s broader hypothesis also mentioned cardiovascular risk, but no cardiovascular result is posted in the results. The record lists two outcome measures, while no secondary outcomes are posted.

The registry does not report the trial’s original sample-size justification, detailed statistical analysis plan, multiplicity strategy, interim analyses, randomization procedure, or the specific roles covered by triple masking. These omissions constrain assessment of prespecification and methods. The posted adverse-event information also lacks detail on timing, severity, relatedness, and event-level circumstances. These limitations call for a narrow reading of the reported BMD comparison and descriptive safety counts.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Use of Rosuvastatin in HIV-Infected Subjects to Modulate Cardiovascular Risks — NCT01218802.
• Registry record last updated 2016-03-08; status last verified 2016-03.
• Results first posted 2016-03-08.
• 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.

21. Record Summary

NCT01218802 is a completed phase 2 randomized, placebo-controlled, triple-masked, parallel trial sponsored by University Hospitals Cleveland Medical Center. The registry reports 147 enrolled participants and compares rosuvastatin 10 mg daily for 96 weeks with a sugar-pill placebo.

The primary outcome was BMD percentage change measured by DEXA from baseline to week 96. The mean change was -0.03 in the rosuvastatin group and -0.53 in the placebo group. The posted mean difference was 0.5, with a confidence interval from -0.449 to 1.449 and an unadjusted p-value of 0.302. Valid outcome data were available for fewer participants than were enrolled.

The registry also posts adverse-event counts, but does not report deaths in the registry record. No secondary outcomes are posted, and the record does not provide the original sample-size justification or detailed analysis plan. The results support a descriptive account of the posted BMD comparison, with substantial limits on what can be concluded beyond that endpoint.