Coronary Artery Revascularization in Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Coronary Artery Revascularization in Diabetes (NCT00326196), a randomized phase 4 study. The primary outcome is The Hypothesis Being Tested is That a Strategy of Initial Surgical Revascularization is Superior to Percutaneous Intervention in Preventing Death or Myocardial Infarction in Diabetics With Severe Ischemic Heart Disease Assessed up to 4 Years..

2. Clinical Question

3. Trial Design

NCT00326196, titled Coronary Artery Revascularization in Diabetes, is the VA CARDS trial. The sponsor was the US Department of Veterans Affairs. The registry record describes a randomized, multi-site clinical trial with a parallel-arm design. It reports no masking. Participants were assigned to percutaneous coronary intervention or coronary artery bypass grafting. The phase is listed as Phase 4.

The record lists enrollment of 198. The posted primary outcome counts are 21.0 participants with an event among 101.0 in the PCI arm and 16.0 among 97.0 in the CABG arm. The record says that the number of participants for analysis was determined by an intent-to-treat principle. It does not give further details about how randomization was generated, how allocation was concealed, or how adherence and crossovers were handled; those details are not reported in the registry record.

The trial start is listed as 2006-07, and primary completion as 2012-08. Its status is terminated. The registry record does not explain the reason for termination, the timing or circumstances of that decision, or whether it affected follow-up or the planned analysis. Monitoring for the primary outcome was described as extending up to 4 years, but the actual follow-up distribution is not reported in the registry record.

The record lists one outcome measure and no posted analyses. It gives counts for the primary binary outcome and an unadjusted comparison, but no analysis population flow, protocol deviations, or detailed statistical analysis plan. The original design assumptions, including any original sample-size rationale, are not reported in the registry record. Therefore, the design can be described as randomized and parallel, but its full operational and analytical details cannot be reconstructed from the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Study participants were were pre-screened by Cath lab. The remaining participants were consented and screened for study eligibility.

Overall Study

Analysis population for the primary outcome, as defined in the registry: The number of participants for analysis was determined by intent to treat principal.

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 The Hypothesis Being Tested is That a Strategy of Initial Surgical Revascularization is Superior to Percutaneous Intervention in Preventing Death or Myocardial Infarction in Diabetics With Severe Ischemic Heart Disease Assessed up to 4 Years., measured over Date of Death and non-fatal MI.

The primary endpoint is a composite of death or myocardial infarction. A participant is counted as having an event if they died or experienced at least one myocardial infarction during monitoring, described as up to 4 years. The outcome measure is the number of participants with an event, and its unit is participants. The registry record identifies the analysis population as determined by an intent-to-treat principle.

A composite endpoint combines clinically distinct events into one outcome. As a general statistical concept, this can capture a broader range of important events and can make an overall comparison more informative than counting only one component. However, a composite result does not show how much each component contributed. For this trial, separate counts for death and myocardial infarction are not reported in the registry record, so the posted combined outcome cannot establish whether the two components followed similar patterns.

The timeframe matters to interpretation: the endpoint concerns events recorded during monitoring of up to 4 years, not a claim that every participant was followed for the same duration. The record does not report the distribution of follow-up or a time-to-event analysis. It describes a count-based binary outcome: each participant either met the event definition or did not, as represented in the posted arm totals. The endpoint is intended to address the trial’s stated comparison of initial surgical and percutaneous revascularization strategies, but the registry record does not supply further detail on outcome adjudication or the definitions used for each component.

7. Results Posted in the Registry

• Coronary Artery Bypass Graft: 16.5% (16/97) versus 20.8% (21/101) on control; risk difference -4.3 percentage points (95% CI -15.1 to 6.5), risk ratio 0.79 (0.44–1.43); unadjusted two-proportion z-test p = 0.438.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: the record counts whether a participant died or had at least one myocardial infarction. A participant meeting either component is counted as having an event. The registry record reports event counts and the number of participants in each arm. In general, a binary outcome can be summarized as an event proportion within each group and compared using measures on either an absolute or relative scale. The record posts both types of comparison, but does not describe every calculation step or its underlying method.

What does a risk difference express?

A risk difference compares the event proportions between groups by subtraction. It is an absolute-scale measure: it describes the contrast in event probability in the units of the outcome proportion. The posted estimate is -0.043 for CABG compared with PCI. The sign depends on the stated comparison order; the estimate is not a separate outcome count. The associated interval, -0.151 to 0.065, represents uncertainty around that estimated contrast under the interval method used. That method is not reported in the registry record.

Absolute measures can be useful because they relate the comparison directly to the difference in event probability. However, the estimate is based on the observed trial data and is not a guarantee about other populations or settings. The confidence interval is essential to interpretation: the point estimate is only one value within a range of values compatible with the data and method.

How do relative measures differ?

The posted relative risk and odds ratio describe the comparison on relative scales. A relative risk compares event proportions as a ratio. An odds ratio compares event odds rather than event proportions. Both are reported with confidence intervals in the registry record. Relative and absolute measures answer related but non-identical questions, and their numerical values should not be compared as if they used the same scale. The registry record does not explain why these particular measures were selected or specify an adjustment model.

For relative measures, a value representing no relative association is the neutral reference. The posted intervals include that reference. For a risk difference, the corresponding neutral reference is zero, which is also included in its posted interval. This is a general interpretation of confidence intervals, not a claim about a prespecified decision rule for this trial. The registry record does not report the original decision threshold or the method used to calculate these intervals.

What does the p-value contribute?

The reported p-value is unadjusted and equals 0.438. In general, a p-value describes how compatible observed data, or data more extreme under a specified model, are with a null hypothesis. It is not the probability that the null hypothesis is true, and it does not state the probability that the result arose by chance. It also does not convey the magnitude or precision of the estimate, so it should be read alongside the point estimate and confidence interval. The registry record does not identify the statistical test, its assumptions, or an adjusted p-value.

The record says there was one outcome measure and lists no posted analyses. It therefore does not present a set of secondary endpoint comparisons or multiple model specifications to assess. Whether additional analyses were conducted outside the posted record is not reported in the registry record. The fact that a comparison is labelled unadjusted does not establish which possible covariates or design features were considered; details of any planned adjustment are not reported.

How should the analysis population be understood?

The registry record states that the number of participants for analysis was determined by an intent-to-treat principle. As a general concept, intent-to-treat analysis aims to retain participants in the groups to which they were assigned, regardless of later treatment received. This helps preserve the comparison created by randomization. The record does not give participant-level flow, exclusions, missing outcome counts, treatment changes, or a detailed account of how the stated principle was implemented. It is therefore not possible to assess those aspects from the posted information.

Random assignment and lack of masking are both recorded design features. Randomization is intended, in general, to reduce systematic differences between assigned groups at baseline. Lack of masking means the record does not describe the trial as blinded; it does not by itself establish whether outcome assessment was affected. The registry record does not report outcome-adjudication procedures or the safeguards used for endpoint assessment.

Why can over-dispersion matter?

General statistical explanation: over-dispersion arises when observed variation is greater than a model assumes. It can make standard errors too small and confidence intervals too narrow if the model does not account for the extra variation. This issue is often relevant to grouped counts or repeated observations. The primary endpoint posted for this trial is a participant-level binary count, and the registry record does not identify a model that assumes a count distribution or report an over-dispersion assessment. It would therefore be inappropriate to assert that over-dispersion affected this analysis.

Overall, the posted statistics support a descriptive account of the comparison: counts by randomized group, an unadjusted risk-difference estimate and interval, relative measures and intervals, and an unadjusted p-value. The registry record does not give enough methodological detail to reproduce the analysis or verify its assumptions independently. Interpretation should distinguish the numerical result from the broader questions that are not answered by the posted analysis, including component-specific effects and differences in follow-up.

10. Confidence Intervals and Precision

The principal measure of precision is the confidence interval around the risk-difference estimate. For CABG compared with PCI, the estimate is -0.043 and the interval runs from -0.151 to 0.065. The interval extends across zero, the value corresponding to no absolute difference. Thus the data are compatible with a range of possible effects that includes a difference favoring either direction as well as no difference. The point estimate alone cannot express this uncertainty.

In general, a confidence interval is a range produced by a statistical procedure that, under its assumptions, reflects uncertainty in an estimate. It is not a guarantee that the true value lies in the particular interval, and it does not assign probabilities to individual values within that interval. The confidence level and calculation method for the posted intervals are not reported in the registry record. The planning significance level listed for illustrative sample-size calculations is not identified as the trial’s original analysis threshold.

The relative risk interval, 0.441 to 1.428, and odds ratio interval, 0.366 to 1.546, also include their respective neutral values. They indicate uncertainty on relative scales, and should not be conflated with the absolute risk-difference interval. No adjusted confidence intervals are reported. There are also no posted intervals for separate death and myocardial-infarction outcomes, and the registry record lists no secondary posted outcomes.

Precision is constrained by the amount of information in the observed groups and by the number of events, but the record does not provide a formal precision target or the original sample-size justification. The enrollment and outcome counts describe the data available in the record; they do not by themselves establish whether the trial was designed to detect a particular effect. The breadth of the posted interval is a reason to avoid treating the point estimate as a precise estimate of the comparative effect.

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 illustrations based on the observed effect, not the trial’s original design calculation. For this binary outcome, the listed figures are participants per arm, not total events. The assumptions stated for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect.

The 80% power column gives the estimated participants per arm for a planning scenario with 80% power under those assumptions. In plain language, power is the probability that a specified statistical procedure will identify an effect of the size being planned for, if that effect is present and the assumptions hold. The 90% power column gives the corresponding per-arm planning estimate for a scenario with 90% power. Higher planned power generally requires more participants for the same target effect.

The listed scenarios are planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The corresponding participants per arm for 80% power are 1,289, 2,342, and 5,382; for 90% power they are 1,725, 3,135, and 7,204. These are illustrative estimates, not observed trial enrollment targets. Smaller effects need more participants to distinguish them from random variation with the same planned power, which is why the smaller-effect scenarios have larger planning estimates.

This is not observed power. The calculation uses the observed effect as a planning reference and does not measure the probability that the completed trial detected a true effect. The original sample-size justification and design assumptions are not reported in the registry record. The estimates should therefore be read as conditional planning illustrations, not as evidence that the trial was or was not adequately sized according to its original plan.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.208; treatment proportion p₁ = 0.165; average p̄ = 0.186.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5508 = 1.0795.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5499 = 0.4628.
4. n = (1.0795 + 0.4628)² / (-0.0430)² = 1,288.2, rounded up to 1,289 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
p0 <- 0.207920792079208                          # control proportion
p1 <- 0.164948453608247                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(326196)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,289 (80% power), 1,725 (90% power)
 75% of observed effect: n per arm = 2,342 (80% power), 3,135 (90% power)
 50% of observed effect: n per arm = 5,382 (80% power), 7,204 (90% power)
power.prop.test: 1288.2 
Simulated power at n = 1,289 per arm: 0.798 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 record lists one outcome measure and no posted analyses. It does not list secondary posted outcomes. The primary outcome combines death and myocardial infarction, while separate results for each component are not reported in the registry record. The record also does not describe a hierarchy of endpoints, a testing sequence, or a prespecified approach to controlling multiplicity.

As a general statistical concept, multiplicity arises when several hypotheses or outcomes are tested. Conducting many tests can increase the chance of at least one result appearing notable by chance, so analysis plans may specify how to interpret or adjust for multiple comparisons. No multiplicity procedure is reported in the registry record. With only one posted outcome measure and no posted analyses, the record does not show whether additional comparisons were planned or conducted elsewhere.

The record identifies an intent-to-treat principle for determining the analysis population, but it does not report missing outcome counts or how missing data were handled. It is not possible to conclude that there were no missing data, or to determine whether any missing observations were excluded, imputed, or addressed through another method. The actual follow-up distribution and participant flow are also not reported in the registry record.

Randomization is reported, but details of allocation generation and concealment are absent. The record lists no masking and does not describe outcome adjudication. It gives an unadjusted p-value, but the statistical test and any prespecified covariate adjustment are not reported. These omissions limit assessment of analytical choices and potential sources of bias. They do not establish that a particular method was or was not used; they mean that the relevant details are not reported in the registry record.

The registry status is terminated. The reason for termination, whether it altered recruitment or follow-up, and any implications for the planned analyses are not reported in the registry record. The design’s original sample-size assumptions, interim analyses, and stopping rules are likewise not reported. Without those details, the posted outcome should be interpreted as the result recorded for the available comparison, not as a complete account of the trial’s planned statistical framework.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: coronary artery stenosis (3.1%), renal failure acute (3.1%), pleural effusion (3.1%), pulmonary oedema (3.1%), chest pain (3.0%).

The registry record reports serious adverse events affecting 23 participants among 101 at risk in the PCI group and 46 among 97 at risk in the CABG group. It reports other adverse events affecting 7 participants among 101 at risk in the PCI group and 67 among 97 at risk in the CABG group. These are reported counts of participants affected, not a comparison adjusted for follow-up or participant characteristics. The record does not explain the definitions or collection procedures behind these categories.

The listed serious adverse-event terms include Coronary artery stenosis, Renal failure acute, Pleural effusion, and Pulmonary oedema, each reported as 3.1%; Chest pain and Cardiac procedure complication are each reported as 3.0%. These terms and percentages should be understood as registry listings, not as evidence that an event was caused by a procedure. The record does not provide detailed event-level attribution or explain whether participants could contribute to multiple terms.

Deaths in the adverse-event record are not reported in the registry record. Safety counts are distinct from the primary composite endpoint, which counts death or myocardial infarction. Differences in adverse-event counts alone do not establish a comparative safety effect because the record does not provide further context on event definitions, ascertainment, or exposure time.

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

The posted comparison documents event counts for a randomized trial of PCI versus CABG in participants with diabetes and significant coronary artery disease. The primary composite endpoint counted death or myocardial infarction during monitoring of up to 4 years. The observed count was 21.0 among 101.0 in the PCI group and 16.0 among 97.0 in the CABG group. The posted risk-difference estimate for CABG compared with PCI is -0.043, with an interval from -0.151 to 0.065 and an unadjusted p-value of 0.438.

These results describe the posted data and the uncertainty around their comparison. The interval includes no difference and values in either direction, so the result does not precisely determine the comparative effect. The relative risk and odds ratio intervals also include their neutral values. The p-value is not a measure of clinical importance and is not the probability that one strategy is superior. None of these statistics, by themselves, proves that either procedure has a particular effect.

The composite endpoint cannot identify whether death or myocardial infarction contributed more to the result because component-specific counts are not reported in the registry record. The posted record also does not provide secondary outcomes, subgroup comparisons, adjusted analyses, or details of outcome adjudication. It cannot answer questions that depend on those data.

The record describes the trial as randomized, multi-site, parallel, and unmasked, with status terminated. It does not explain the termination or report the original analysis plan, sample-size rationale, missing-data handling, or actual follow-up distribution. These limits matter when assessing how far the posted estimates can be generalized or connected to the intended study design. The result is best read as an uncertain, unadjusted comparison of the recorded groups, rather than as a definitive conclusion about the relative merits of the procedures.

16. Why This Trial Matters Statistically

This trial addresses a consequential statistical challenge: comparing two revascularization strategies using a composite endpoint that combines death and myocardial infarction. Random allocation provides a basis for comparing assigned groups, while the recorded intent-to-treat principle aims to preserve that assignment-based comparison. The trial therefore illustrates how a clear clinical question can be expressed through a defined binary endpoint and a contrast between randomized arms.

It also illustrates why a point estimate cannot stand alone. The observed risk-difference estimate is accompanied by an interval extending across zero, while the relative-measure intervals include their neutral values. Those intervals show that the posted data leave substantial uncertainty about the direction and magnitude of the comparison. A p-value adds a different kind of statistical summary, but it does not replace the effect estimate or its precision.

The record’s limited outcome reporting also highlights the interpretive cost of a composite endpoint when component results are absent. A combined event count gives an overall endpoint result, but does not reveal whether death and myocardial infarction had similar patterns. Likewise, posted adverse-event counts require caution when definitions, attribution, exposure time, and event-level overlap are not described.

Finally, the trial record distinguishes results from design information. It lists a terminated status and no posted analyses beyond the primary outcome, while the reason for termination and original statistical assumptions are not reported in the registry record. Planning illustrations based on the observed effect cannot stand in for the trial’s original justification. For statistical readers, the case underscores the value of transparent reporting of analysis plans, missingness, follow-up, endpoint components, and precision alongside point estimates.

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.

Several limitations specific to this trial follow from what the registry record does and does not report. The status is terminated, but the reason, timing, and consequences are not reported. It is not possible to determine from the record whether termination affected enrollment, follow-up, or the analysis. The trial lists enrollment of 198, but no original sample-size justification is reported. Planning illustrations based on the observed effect do not resolve that gap.

The primary result is a composite of death or myocardial infarction. Separate component counts are not reported, so the combined outcome does not show which component contributed to the observed event counts. The record describes monitoring for up to 4 years but does not provide the actual follow-up distribution or a time-to-event analysis. The posted comparison is therefore a count-based binary result, without a reported account of how differing follow-up was addressed.

The record identifies an intent-to-treat principle but does not give participant flow, outcome missingness, crossovers, adherence, or the detailed implementation of that principle. It lists a randomized, unmasked design but does not describe sequence generation, allocation concealment, endpoint adjudication, or possible safeguards for assessment. These details are not reported in the registry record, so their use or absence cannot be inferred.

Only one outcome measure and no analyses are listed beyond the posted primary comparison. There are no reported secondary outcome results, adjusted models, subgroup analyses, or multiplicity procedures. The unadjusted p-value is posted, but its test and assumptions are not reported. These omissions limit independent evaluation of analysis choices and the scope of evidence available from the registry record. They should be treated as reporting limitations, not as proof that additional methods or data were absent from the conduct of the trial.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Coronary Artery Revascularization in Diabetes — NCT00326196.
• Registry record last updated 2014-04-25; status last verified 2014-04.
• Results first posted 2014-02-06.
• 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

NCT00326196 is the VA CARDS randomized, multi-site, parallel trial comparing PCI with CABG for coronary artery disease in participants with diabetes. It was sponsored by the US Department of Veterans Affairs, listed as Phase 4, unmasked, and terminated. Enrollment was 198. The trial start is recorded as 2006-07 and primary completion as 2012-08.

The primary endpoint was death or myocardial infarction, monitored for up to 4 years. The registry record reports 21.0 events among 101.0 participants in the PCI arm and 16.0 among 97.0 in the CABG arm. The unadjusted risk-difference estimate was -0.043, with a confidence interval from -0.151 to 0.065 and an unadjusted p-value of 0.438. The record lists one outcome measure and no posted analyses.

The record states an intent-to-treat principle, but does not report the original sample-size rationale, detailed analysis plan, missing-data handling, or reason for termination. The posted comparison should be interpreted alongside those reporting limits and the uncertainty reflected in its confidence interval.