Simvastatin Therapy for Moderate and Severe COPD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Simvastatin Therapy for Moderate and Severe COPD (NCT01061671), a randomized phase 3 study. The primary outcome is Rates of COPD Exacerbations.

2. Clinical Question

The central comparison is between the mean exacerbation rates recorded in the simvastatin and placebo groups. A person-year rate expresses events in relation to time observed, rather than simply counting events across groups with potentially different follow-up. This makes it a useful way to summarize recurrent exacerbations over a period of follow-up.

The registry identifies the study as a prospective randomized placebo-controlled trial, with triple masking and a parallel-group model. The primary outcome description specifies an analysis population that excludes participants without follow-up data. The registry record does not report further detail about how the analysis handled participants with incomplete follow-up or how the treatment duration varied among participants.

3. Trial Design

The trial, titled Simvastatin Therapy for Moderate and Severe COPD, is listed as a phase 3, randomized, triple-masked, parallel-group study. It compared daily simvastatin with a matched placebo. The stated purpose was to evaluate the effect of daily simvastatin on COPD exacerbation frequency among people with moderate to severe disease who were prone to exacerbations and had no other indication for statin treatment.

The registry records enrollment of 885. The primary completion date is listed as 2014-01, and the study status is terminated. The planned treatment description specifies 40 mgms of simvastatin daily for at least 12 months, with a range of 12-36 months; the placebo arm received a matched pill daily. The primary outcome timeframe is described as up to 37 months.

Randomization supports a comparison of outcomes between assigned groups, while masking is intended to limit influences of treatment knowledge on participant care, reporting, and assessment. The record identifies triple masking but does not specify which roles were masked. The parallel design means the groups were followed as separate treatment arms, rather than participants crossing from one treatment to the other.

The registry lists secondary outcomes concerning time to first COPD exacerbation, change in FEV1 (% Pred) from baseline to last measure, and COPD hospitalization rates. The record does not report the trial's original sample-size justification, detailed allocation procedures, or the original statistical analysis plan. Those design details should not be inferred from the posted results or from planning illustrations based on observed data.

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: Analysis excludes participants without any follow-up data.

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 Rates of COPD Exacerbations, measured over up to 37 months.

The primary endpoint is the rate of COPD exacerbations, expressed as exacerbations per person-year, over up to 37 months. It is reported as a mean with standard deviation in each group. Unlike a simple count of participants who experience at least one exacerbation, a rate can reflect repeated events and the amount of time participants contribute to observation.

Rates are useful when participants may have different lengths of follow-up or may experience more than one event. The person-time denominator places event counts in relation to observed time, making the groups' event frequency easier to compare on a common scale. A mean rate, however, does not by itself describe the full distribution of recurrent events. Some participants may have no exacerbations, while others may have multiple events, so the average can conceal variation between individuals.

The outcome description says that participants without any follow-up data were excluded from the analysis. The posted group summaries give the mean rate and standard deviation, while the registry also reports a negative binomial regression analysis. These are related ways to study event frequency, but they do not provide identical summaries: the group means describe observed rates, whereas the regression analysis models event counts in relation to follow-up time.

7. Results Posted in the Registry

• Simvastatin: mean 1.36 versus 1.39 on control; difference -0.03 (95% CI -0.25 to 0.19), standardized effect d = -0.02; z-test p = 0.790.

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.

Acute Exacerbation COPD Hospitalization Rates (Events/Patient Year)

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Simvastatin: 0.31 versus 0.31 (events per patient year) on control; rate ratio 1.00 (95% CI 0.71–1.41, derived from the posted confidence limits); p ≈ 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Simvastatin and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies secondary outcomes involving time to first COPD exacerbation, change in FEV1 (% Pred), and COPD hospitalization rates. The available record does not report detailed results for every listed secondary outcome, so a comprehensive assessment of whether all secondary endpoints point in the same direction is not possible.

The posted hospitalization-rate summaries show similar group point estimates, and the rate-ratio interval includes 1. This is broadly consistent with the primary summaries not showing a clear separation, but the endpoint measures a different aspect of COPD events: hospitalizations rather than all exacerbations. It should not be treated as a substitute for the primary endpoint or as independent confirmation of it.

Secondary outcomes are usually interpreted more cautiously because trials may assess several outcomes, creating more opportunities for apparently notable results to arise by chance. The registry record does not report whether or how multiplicity was addressed. Without that information, unadjusted secondary results carry less weight as confirmatory evidence, particularly when their estimates are imprecise or when results for other endpoints are unavailable. The secondary outcomes can provide context, but they do not resolve the uncertainty around the primary comparison.

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

• Time to First COPD Exacerbation
• Change in FEV1 (% Pred) From Baseline to Last Measure
• Acute Exacerbation COPD Hospitalization Rates (Events/Patient Year)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results combine group-level summaries with a model-based analysis. These approaches answer related but not identical statistical questions. Reading them together requires attention to what each estimate represents, how uncertainty is expressed, and which analysis the registry identifies as the reported analysis.

What does the mean difference describe?

The primary group summaries report mean exacerbation rates in each arm. The recalculated mean difference subtracts the placebo mean from the simvastatin mean, so negative values indicate a lower observed mean rate in the simvastatin arm. The posted difference is -0.03 exacerbations per person-year. This is an unadjusted comparison of the posted summaries; it does not incorporate covariate adjustment or the full participant-level event histories.

The standard deviations describe variation in observed rates within each group. They are not standard errors and do not directly measure how precisely the group means are estimated. Standard errors reflect uncertainty in an estimate and are smaller or larger depending on both variability and the amount of information available. The recalculated comparison uses the posted group summaries to estimate uncertainty around the mean difference.

Why use a negative binomial model?

Event-count data often vary more across individuals than a simple Poisson model would allow. This is called over-dispersion: the variability in counts exceeds the level expected under the simpler model. A negative binomial regression can accommodate this extra variation and can model recurrent events while accounting for follow-up time. In general, such a model can also include explanatory variables, although the registry record does not report which variables, if any, were included in this analysis.

The registry identifies negative binomial regression as the method for the reported primary analysis and gives p = 0.54. It does not provide the model's estimated effect, confidence interval, covariate specification, or other details needed to reproduce the analysis. The result therefore conveys the reported test result but does not, on its own, show the estimated magnitude or precision of the model-based treatment contrast.

How should the p values be read?

A p value measures how unusual data at least as incompatible with a specified null hypothesis would be under the assumptions of a statistical model. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. The recalculated unadjusted comparison has p = 0.79, while the reported negative binomial analysis has p = 0.54. Because they arise from different methods, the values are not interchangeable. Neither one states the probability that treatment has no effect.

A test result should be considered alongside the estimated effect and its confidence interval. For the unadjusted mean difference, the interval extends from -0.251 to 0.191. The range includes the null value of zero and also includes values on both sides of zero. This indicates uncertainty about the direction and size of the difference under that calculation. The registry does not report a confidence interval for the negative binomial result, so its precision cannot be assessed from the reported p value alone.

What does the hospitalization rate ratio represent?

The secondary hospitalization outcome is expressed as events per patient-year. The rate ratio compares the event rates between groups; a value of 1.0 corresponds to equal point estimates. Its reported interval, from 0.712 to 1.405, describes uncertainty in the comparison. The registry also gives confidence intervals for the group rates themselves. These intervals are not confidence intervals for a difference between groups: each one concerns its own group's rate.

These methods describe statistical summaries, not causation in isolation. Randomized allocation supports a treatment-group comparison, but interpretation also depends on outcome ascertainment, missing data, adherence, and the analysis population. The registry record does not report all details needed to evaluate these issues fully. Accordingly, the posted results can be interpreted as evidence from the documented comparisons, while unreported modeling and data-handling choices remain unknown.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty around an estimate under the analysis method used. It is not a guarantee that the true effect lies within the interval, nor does it assign a probability to each possible value. Wider intervals indicate less precision; narrower intervals indicate greater precision, conditional on the assumptions of the method.

For the unadjusted primary mean difference, the posted estimate is -0.03 exacerbations per person-year, and the 95% confidence interval ranges from -0.251 to 0.191. Because this interval includes zero, the data do not pin down the direction of the mean difference. Values indicating a lower rate in the simvastatin group and values indicating a higher rate are both compatible with the interval. The point estimate is close to zero, but that alone is not enough to conclude the groups are equivalent.

For the secondary hospitalization rate ratio, the estimate is 1.0 and its 95% confidence interval ranges from 0.712 to 1.405. The interval includes 1, the value corresponding to equal rates, and also allows for relative differences in either direction. The group-specific rate intervals are 0.24 to 0.38 for simvastatin and 0.23 to 0.38 for placebo. Overlap between group-specific intervals is not itself a formal test of the difference between groups; the rate-ratio interval addresses that comparison more directly.

The registry does not report a confidence interval for the negative binomial regression result. Its p value therefore cannot substitute for an interval when judging the model-based estimate's precision. In general, a p value alone gives limited information about the range of effects compatible with the data.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design assumptions. They are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

The 80% power column means that, under those assumptions and if the specified effect were the true effect, the design would have an 80% chance of producing a statistically significant result. The 90% power column describes the corresponding chance as 90%. These are planning targets, not guarantees. The calculations do not describe the trial's achieved probability of detecting an effect after the results were observed.

Rows that plan for a smaller fraction of the observed effect require more participants per arm than rows planning for a larger effect. Smaller effects are harder to distinguish from random variation, so more information is generally needed to detect them with the same target power. The displayed figures rise as the assumed detectable effect becomes smaller, and the 90% target requires more participants per arm than the 80% target for a given effect assumption.

These figures are sample-size planning illustrations, not observed power. They should not be read as evidence that the trial was adequately or inadequately sized under its own design, because the original sample-size justification and planning assumptions are not reported in the registry record. The posted calculations are tied to the observed effect and their listed assumptions, so they are sensitive to the uncertainty in that observed estimate.

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 = -0.030; pooled standard deviation σ = 1.672.
2. n = 2 × (1.96 + 0.842)² × 1.672² / -0.030² = 48,774.6, rounded up to 48,775 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 <- -0.0299999999999998                      # observed difference in means
sigma <- 1.6722420535659                     # 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(1061671)
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 = 48,775 (80% power), 65,296 (90% power)
 75% of observed effect: n per arm = 86,711 (80% power), 116,081 (90% power)
 50% of observed effect: n per arm = 195,099 (80% power), 261,182 (90% power)
power.t.test: 48775.5 
Simulated power at n = 48,775 per arm: 0.797 (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

The registry reports the primary comparison using negative binomial regression, with p = 0.54. The reported analysis does not include an effect estimate or confidence interval in the record. The unadjusted recalculation from the posted group means gives a mean difference of -0.03 exacerbations per person-year, a 95% confidence interval from -0.251 to 0.191, and p = 0.79.

These results come from different statistical approaches. The recalculation uses the group-level means and standard deviations, whereas negative binomial regression models event counts and can account for follow-up time and over-dispersion. A difference between their p values is not, by itself, evidence that one calculation is erroneous. The regression result is the sponsor's reported analysis; the recalculation is a separate, unadjusted check based on posted summary statistics.

The registry record does not give enough detail to reproduce the regression model or compare its estimate directly with the recalculated mean difference. In particular, it does not report the regression effect estimate, confidence interval, or model specification. The results should therefore be kept distinct rather than treated as competing estimates of precisely the same quantity.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome description specifies an analysis population that excludes participants without any follow-up data. The registry record does not report how many participants had no follow-up, how many had partial follow-up, or how missing outcome information was handled beyond that stated exclusion. It also does not specify whether other analysis populations were used, such as an intention-to-treat population, or how adherence and treatment changes were addressed.

These details matter because excluding participants with no follow-up can affect the composition of the analyzed groups if follow-up availability is related to health status, treatment, or outcome risk. Randomization establishes the initial comparison, but missing outcome data can weaken its protection if the reasons for missingness differ between groups or relate to the outcome. The registry does not provide enough information to assess whether such concerns arose in this trial.

The record lists multiple outcomes and analyses, but does not report a multiplicity strategy. When several endpoints or comparisons are examined, the chance of finding at least one apparently unusual result can increase. Prespecifying a primary endpoint and an analysis hierarchy can help clarify which findings are confirmatory and how secondary results should be interpreted. Whether such procedures were used is not reported in the registry record.

The registry also does not report interim analyses, stopping rules, or detailed handling of repeated events in the analysis plan. These should not be inferred from the status of the study or from the posted results. Without a fuller protocol or statistical plan in the record, interpretation is limited to the outcome definitions and analyses that are documented.

16. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: copd exacerbation (22.2%), pneumonia (7.9%), other respiratory (2.9%), ill defined respiratory events (2.9%), other digestive disorders (2.5%).

The adverse-event record lists serious adverse events for participants at risk in each arm. For simvastatin, 178 of 433 participants at risk were recorded as affected; for placebo, 190 of 452 were recorded as affected. These are counts of participants recorded as affected, not counts of distinct event episodes. The registry also lists other adverse events: 316 of 433 participants at risk in the simvastatin arm and 329 of 452 in the placebo arm.

The listed serious-event terms include COPD exacerbation, pneumonia, other respiratory events, ill-defined respiratory events, other digestive disorders, and respiratory cancer. The record presents percentages for these terms but does not provide enough detail in the listing to establish a complete arm-by-arm comparison for each term. Death counts are not reported.

These figures should be read as descriptive safety reporting, not as a causal comparison or a full assessment of risk. The registry record does not give event timing, severity detail beyond the serious classification, exposure-adjusted rates, or the methods used to determine relatedness. Differences in raw counts alone do not account for differences in group size or follow-up time, and should not be interpreted as evidence for or against a treatment effect.

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

The posted primary summaries show very similar mean exacerbation rates between the simvastatin and placebo groups, with an unadjusted difference close to zero and an interval that includes effects in either direction. The registry's reported negative binomial analysis also does not provide a statistically significant p value under its reported test. Together, these findings do not establish a clear difference in the primary outcome in the posted analyses.

That interpretation is not the same as proving that the treatments are equivalent, or that no meaningful difference is possible. The unadjusted confidence interval includes a range of effects, and the model-based result is reported without an effect estimate or interval. The precision and practical importance of the regression estimate therefore cannot be judged fully from the registry record.

The trial concerns a specific population: people with moderate to severe COPD who were prone to exacerbations and had no other indication for statin treatment. The record does not justify extending the results to people with different characteristics, different treatment indications, or a different pattern of follow-up. The posted results also cannot establish effects on outcomes that were not reported in sufficient detail.

Safety counts are descriptive and do not by themselves establish whether an adverse event was caused by a treatment. The record's serious-event summaries should be considered alongside the outcome findings, while recognizing that timing, exposure, and event attribution details are not reported. Overall, the statistics describe the observed trial comparisons and their uncertainty; they do not provide medical advice or determine an individual's treatment choice.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of statistical method matters for recurrent clinical events. An average rate provides an accessible group summary, while negative binomial regression is designed to analyze event counts when participants may experience repeated events and variability may exceed that expected under a simpler count model. The two methods can yield different test statistics because they use information differently and may target related but distinct quantities.

It also shows why effect estimates and confidence intervals are important alongside p values. A p value summarizes evidence against a null model under specified assumptions; it does not show the magnitude of a difference or how precisely that magnitude is estimated. The unadjusted mean difference and its interval offer more direct information about the scale and uncertainty of that comparison. The reported regression p value, without an accompanying estimate or interval, is less informative about the model-based effect's precision.

Rates per person-year are useful for recurrent outcomes observed over time, but their interpretation depends on follow-up and the distribution of events. The primary analysis excludes participants without any follow-up data, and further details about missingness are unavailable. This highlights the importance of prespecified analysis populations, transparent reporting, and clarity about how incomplete observation is handled.

Finally, the secondary outcomes and safety summaries illustrate the limits of registry reporting. Several outcomes are listed, but the record does not contain full results or a stated multiplicity approach. Statistical interpretation depends not only on calculations but also on complete reporting of the analysis plan, estimates, uncertainty, and missing-data decisions.

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 registry record leaves important analytic details unreported. It does not give the negative binomial model's effect estimate or confidence interval, its covariates, or enough specification to reproduce the analysis. The reported p value alone cannot communicate the size or precision of the model-based comparison.

The primary endpoint description excludes participants without follow-up data, but the record does not describe the extent or handling of missing follow-up beyond that exclusion. It also does not provide detailed adherence information, treatment discontinuation patterns, or the analysis population definitions beyond the primary outcome note. These gaps limit assessment of how closely the posted comparison preserves the randomized groups.

Although the registry lists secondary outcomes, detailed results are not available for all of them in this record. It does not report whether multiplicity was addressed, nor does it provide the original sample-size justification, interim analysis plans, or detailed stopping rules. The planning illustrations based on the observed effect cannot replace those original design details.

The adverse-event summary is also limited: death counts are not reported, and the record does not describe event timing, exposure-adjusted comparisons, or attribution procedures. The trial is listed as terminated, but the registry record does not explain the reason. No reason should be inferred from the status alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Simvastatin Therapy for Moderate and Severe COPD — NCT01061671.
• Registry record last updated 2018-01-02; status last verified 2017-12.
• Results first posted 2015-03-26.
• 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

NCT01061671 is a phase 3 randomized, triple-masked, parallel-group trial comparing daily simvastatin with matched placebo in people with moderate to severe COPD who were prone to exacerbations and had no other indication for statin treatment. Enrollment is listed as 885; the study status is terminated, and primary completion is recorded as 2014-01.

The primary outcome is mean COPD exacerbation rate per person-year over up to 37 months, with participants without follow-up data excluded. The posted means are 1.36 for simvastatin and 1.39 for placebo. The unadjusted mean difference is -0.03, with a 95% confidence interval from -0.251 to 0.191. The registry reports negative binomial regression with p = 0.54, but does not include its effect estimate or confidence interval.

The record also lists secondary outcomes and adverse-event summaries, with important analytic and missing-data details not reported.