Glycemic Control to Prevent Cardiac Morbidity in Vascular Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Glycemic Control to Prevent Cardiac Morbidity in Vascular Surgery (NCT00328094), a randomized na study. The primary outcome is Composite (Myocardial Infarction and CHF).

2. Clinical Question

The study summary frames the broader question around perioperative cardiac outcomes and secondary outcomes such as infections, overall morbidity, and 30-day mortality. The posted secondary outcome is incidence of wound infections. Results for overall morbidity and 30-day mortality are not reported in the registry record. The listed primary endpoint is a combined outcome: the posted information does not separate myocardial infarction from congestive heart failure, so the contribution of each component cannot be assessed from these results.

3. Trial Design

The registry identifies NCT00328094 as a randomized, single-masked, parallel-group study sponsored by Beth Israel Deaconess Medical Center. Its enrollment is listed as 242. The trial status is terminated. The recorded study start is 2006-03, and primary completion is recorded as 2008-04. The reason for termination is not reported in the registry record.

The two arms were continuous insulin infusion and intermittent insulin bolus. The arm descriptions state that both approaches targeted a blood glucose level of <150 mg/dL, although the intermittent-bolus description writes the unit without a space before it. The setting described for these arms is peripheral vascular bypass surgery, with open bypass specified for the continuous-infusion arm. The broader study summary refers to patients undergoing vascular surgery and includes diabetic and non-diabetic patients.

The registry identifies the design as parallel-group and randomized but does not report the randomization sequence method, allocation concealment, or the allocation ratio. Single masking is recorded, but which participants, clinicians, outcome assessors, or other personnel were masked is not reported in the registry record. The trial phase is listed as NA.

The primary endpoint was the composite of myocardial infarction and congestive heart failure during the hospital length of stay. The registry also lists postoperative wound infection as a secondary outcome. Although the study summary describes interest in overall morbidity and 30-day mortality, results for those outcomes are not reported in the registry record. The posted arm counts for the primary outcome are 114 in the continuous-infusion arm and 122 in the intermittent-bolus arm; these are the endpoint denominators and should not be treated as a description of every analysis population without further 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.

Before assignment: 252 were assessed for eligibility. 10 did not meet inclusion criterion.

Overall Study

Reasons for not completing this period:

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: assessed for eligibility 252. 10 were found ineligible. 242 were randomized.6 patients did not receive interventions they were supposed to. Total number of patients analyzed were 236.

6. Primary Endpoint

The registry lists the primary outcome as Composite (Myocardial Infarction and CHF), measured over hospital length of stay.

The primary endpoint counts patients with a composite event consisting of myocardial infarction and congestive heart failure during the hospital length of stay. A composite endpoint combines multiple clinical events into one outcome. It can capture whether a participant experienced at least one component, but it does not by itself show which component occurred or whether one component accounts for most of the observed difference. The registry reports only the combined counts, so component-specific results are not reported in the registry record.

The endpoint is expressed as a number of patients with an event, with the arm denominators also posted. This makes the comparison a binary-outcome comparison at the participant level: a patient either had a recorded composite event or did not. The timeframe is the hospital length of stay, rather than a fixed follow-up period reported for all patients. Differences in length of stay could therefore matter to the opportunity to observe an in-hospital event, but the registry record does not provide stay-length details or an analysis of this issue.

In general, combining outcomes can be useful when the components are related to the clinical question and individually uncommon, but the components should also be examined separately when possible. The registry record does not report component-specific estimates, definitions of each event, or information about how events were adjudicated. Those details limit assessment of how the composite was constructed and how consistently it was measured.

7. Results Posted in the Registry

• Intermittent Insulin Bolus: 12.3% (15/122) versus 3.5% (4/114) on control; risk difference 8.8 percentage points (95% CI 2.1 to 15.5), risk ratio 3.50 (1.20–10.25); unadjusted two-proportion z-test p = 0.013.

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.

Incidence of Wound Infections

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Intermittent Insulin Bolus: 23.8% (29/122) versus 30.7% (35/114) on control; risk difference -6.9 percentage points (95% CI -18.3 to 4.4), risk ratio 0.77 (0.51–1.18); unadjusted two-proportion z-test p = 0.231.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intermittent Insulin Bolus and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is postoperative wound infection. The overall pattern is not the same as the primary result: the wound-infection comparison has an interval that includes its null value, while the recalculated primary risk-difference interval lies above zero. These outcomes concern different events and should not be combined into a single conclusion about all postoperative morbidity. The registry record does not report results for the broader secondary outcomes mentioned in the study summary, including overall morbidity and 30-day mortality.

Secondary outcomes generally play a supporting role because they are not necessarily the main basis for evaluating the study question. If several outcomes or comparisons are examined, some may appear notable by chance even when there is no underlying difference. Adjusting for multiplicity or defining a hierarchy among outcomes can help manage that issue, but the registry record does not report a multiplicity strategy. The posted wound-infection result is therefore best treated as exploratory or supportive evidence unless a prespecified analysis plan establishes a different status.

The secondary record includes a reported Chi-squared analysis and its risk ratio, interval, and p-value. Those results should be read as a separate analysis rather than as a test of whether the primary finding is valid. A secondary endpoint can be imprecise even when the primary endpoint appears more distinct, and a result that does not meet a conventional significance threshold does not establish that the groups have identical risks. Conversely, one endpoint's result cannot be used to claim a consistent pattern across outcomes that were not reported.

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

• Incidence of Wound Infections

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a binary-outcome comparison because the endpoint records whether each patient experienced the composite event during the hospital stay. The posted analysis gives the event count and the number of patients at risk in each arm. A risk is the proportion of patients in an arm who had the event over the stated timeframe; a risk difference compares the two arm risks by subtraction. The risk difference reported for intermittent bolus relative to continuous infusion is 0.088, with an interval from 0.021 to 0.155.

This is an unadjusted recalculation from the posted summary counts. An unadjusted comparison uses the arm-level event counts without accounting for other patient characteristics or stratification factors. It is easy to interpret, but it cannot show whether adjustment for baseline factors would change the estimate. The registry record does not report an adjusted primary estimate or the detailed primary analysis method. The discrepancy indicator is false, so the posted summary-derived result does not conflict with a reported sponsor analysis.

In general, a risk difference is an absolute measure of contrast on the outcome scale. A risk ratio instead compares the risks as a ratio, and an odds ratio compares the odds. These measures answer related but not identical questions and can differ in numerical size, especially when outcomes are not rare. The recalculated primary comparison also lists a risk ratio of 3.504 with an interval from 1.198 to 10.25 and an odds ratio of 3.855 with an interval from 1.24 to 11.99. They are alternative summaries of the same observed counts, not independent results. The risk difference remains a direct way to describe the absolute contrast between arms.

A p-value describes how unusual data at least as discordant with a specified null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, nor does it quantify the clinical importance of an effect. The unadjusted primary p-value is 0.013. Its interpretation depends on the comparison being appropriate and on the analysis having been selected without unreported outcome-selection or multiplicity issues. The registry record does not report enough of the original statistical plan to establish those details.

A confidence interval gives a range of estimates compatible with the data under the method used. Its width reflects both the size of the observed effect and the amount of information in the data, along with the method's assumptions. The primary interval ranges from 0.021 to 0.155 for the risk difference. Since it lies on the positive side of zero, the interval is consistent with a positive risk difference for intermittent bolus relative to continuous infusion. The range also indicates that the exact magnitude is uncertain. The confidence level and interval-construction method for this recalculated primary interval are not reported in the registry record.

The posted secondary analysis uses a risk ratio for wound infection. The registry reports a Chi-squared method, a risk ratio of 1.29, a 95% interval from 0.85 to 1.97, and p = 0.23. A Chi-squared test assesses whether observed category counts are consistent with independence, here corresponding to no association between arm and the binary outcome under the test's assumptions. The listed result is not a primary endpoint analysis, and it does not establish equivalence. In general, a nonsignificant test may reflect a small or absent difference, limited precision, or both.

The registry also posts planning illustrations based on observed effects. In general, power is the probability that a planned test will reject a null hypothesis when a particular effect is true, conditional on the assumptions used to plan the study. A power calculation is forward-looking; it does not measure how likely the observed result was after the trial. These illustrations use the observed effect and selected fractions of that effect, with equal allocation and a normal approximation. The trial's own original sample-size justification and design assumptions are not reported in the registry record.

For binary outcomes, over-dispersion is not the central issue in the same way it can be for count outcomes modeled with a Poisson distribution. More generally, over-dispersion means that outcome variability exceeds what a model assumes. If it is ignored in a setting where it matters, standard errors can be too small and intervals too narrow. The registry record does not describe an over-dispersion model for these endpoints, and no such model should be inferred from the posted results.

Randomized trials are often analyzed according to the groups to which participants were assigned, regardless of adherence; this is commonly called intention-to-treat analysis. The registry record does not report whether the primary or secondary analyses followed that principle, how withdrawals or missing outcome data were handled, or whether any patients were excluded after randomization. Thus the posted denominators should be interpreted as the denominators attached to these outcome results, not as proof of a particular analysis population.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.088, with an interval from 0.021 to 0.155. The interval is entirely above zero, matching the direction of the observed contrast: the posted primary event count is lower in the continuous-infusion arm than in the intermittent-bolus arm. The interval's lower and upper limits are materially separated, so the data do not pin down a single exact magnitude. The confidence level and calculation method for this recalculated interval are not reported in the registry record.

Confidence intervals are useful because they show a range of estimates compatible with the observed data under the calculation method, rather than only a single point estimate. In general, an interval that excludes the null value is consistent with a statistically detectable difference at the corresponding confidence level. For a risk difference, the null value is zero. This general interpretation does not make the interval a range containing the true effect with certainty, and it does not address sources of bias or limitations in how outcomes were collected.

The primary ratio estimates are 3.504 for the risk ratio and 3.855 for the odds ratio, with respective intervals from 1.198 to 10.25 and from 1.24 to 11.99. Their intervals are broad, indicating substantial uncertainty around the relative-scale estimates. Because these estimates use a different scale from the risk difference, their numerical sizes should not be compared as if they were the same quantity.

For wound infection, the reported risk ratio is 1.29 with a 95% interval from 0.85 to 1.97. This interval includes the null value for a ratio, and p = 0.23. The result is compatible with a range of contrasts, including no difference; it does not demonstrate that the arms are equivalent. In general, evidence for equivalence requires a prespecified margin and an analysis designed to assess that margin. Such a margin is not reported in the registry record.

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 participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. For binary outcomes in these illustrations, each value is a planned number of participants in each arm under the stated assumptions. The registry's assumptions for the illustrations 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 the stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column means that, if the assumed effect and planning conditions were correct, a study of the listed size in each arm would have an 80% probability of rejecting the null hypothesis using the specified test. The 90% power column describes the corresponding probability as 90%. These are planning probabilities, not guarantees that a result will be statistically significant, and they depend on the assumed effect and other calculation conditions. This is not observed power.

The rows for 100% of the observed effect use the full effect estimated from the posted data; the rows for 75% and 50% use smaller assumed effects. Smaller effects are harder to distinguish from random variation and therefore need more participants to achieve the same planned power under otherwise similar assumptions. These values are illustrations based on the observed trial effect, not evidence that the original study was designed with those targets. The registry record does not report whether the trial's termination was related to recruitment, a planned stopping rule, or any other sample-size consideration.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.035; treatment proportion p₁ = 0.123; average p̄ = 0.079.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3815 = 0.7477.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3764 = 0.3168.
4. n = (0.7477 + 0.3168)² / (0.0879)² = 146.8, rounded up to 147 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 <- 0.0350877192982456                          # control proportion
p1 <- 0.122950819672131                          # 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(328094)
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 = 147 (80% power), 197 (90% power)
 75% of observed effect: n per arm = 229 (80% power), 305 (90% power)
 50% of observed effect: n per arm = 437 (80% power), 584 (90% power)
power.prop.test: 146.8 
Simulated power at n = 147 per arm: 0.819 (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.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, time points, or subgroups are tested. In general, the more tests conducted, the greater the chance that at least one will appear statistically notable by chance if all null hypotheses are true. A prespecified primary endpoint can help focus interpretation, while secondary outcomes can add context, but the strategy for controlling or interpreting multiple tests should be clear.

The registry identifies a primary composite endpoint and lists wound infection as a secondary outcome. The study summary also mentions infections, overall morbidity, and 30-day mortality as secondary areas of interest, but posted results for overall morbidity and 30-day mortality are not reported in the registry record. A multiplicity adjustment, testing hierarchy, or statement that secondary analyses were exploratory is not reported in the registry record. The wound-infection p-value should therefore not be interpreted as if it arose from an explicitly documented family of tests with known error control.

Missing-data handling is also not reported in the registry record. The posted arm denominators are 114 and 122 for the primary outcome and are also the denominators listed for wound infection. Those counts do not establish whether all randomized participants had complete follow-up, whether any outcomes were imputed, or whether exclusions occurred. The registry does not report a flow of participants through the trial, reasons for missing outcomes, or sensitivity analyses addressing missingness.

The analysis population is not described in sufficient detail to determine whether analyses were intention-to-treat, per protocol, or based on another definition. In general, intention-to-treat analysis preserves the randomized group assignment for participants, while per-protocol analysis focuses on those meeting specified adherence criteria. Each approach answers a somewhat different question and can be vulnerable to different biases. No analysis-population definition should be inferred from the posted denominators alone.

The registry record also does not report a detailed statistical analysis plan, covariate adjustment strategy, subgroup plan, or interim-analysis procedure. These details affect how confidently readers can distinguish prespecified analyses from analyses selected after results were known. The absence of these details does not prove that no such procedures existed; it means they are not reported in 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypoglycemia (8.8%).

The registry lists serious adverse events for 10 participants in the continuous-infusion arm, with 114 at risk, and 5 participants in the intermittent-bolus arm, with 122 at risk. Other adverse events are listed for 23 participants in the continuous-infusion arm and 22 in the intermittent-bolus arm, with the same respective at-risk counts. These are arm-level safety figures; the registry record does not provide definitions of the event categories, event-level detail, or a statistical comparison for these counts.

Hypoglycemia is listed as the top serious adverse event term at 8.8%. The record does not provide further detail on its severity, timing, recurrence, or the arm-specific distribution of that term. Death counts are not reported in the registry record. These safety listings should not be treated as a complete account of all harms, because the registry does not describe ascertainment methods, follow-up completeness, or whether multiple events in a participant were counted separately.

In general, counts of participants with adverse events describe what was recorded during the reported safety period; they do not by themselves establish causation or comparative risk. Interpretation also depends on event definitions and the completeness of surveillance, details not reported in the registry record.

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

The posted primary results describe an observed difference in the hospital-stay composite of myocardial infarction and congestive heart failure between the two randomized arms. There were 4 recorded composite events among 114 patients assigned to continuous insulin infusion and 15 among 122 assigned to intermittent insulin bolus. The unadjusted risk-difference estimate is 0.088, with an interval from 0.021 to 0.155 and p = 0.013. These figures characterize the recorded data and their statistical uncertainty under the recalculation method.

They do not establish that the intervention will produce the same result in other surgical populations, care settings, or follow-up periods. The registry record does not report baseline characteristics, component-specific outcome counts, detailed outcome definitions, or how masking was implemented. Those omissions limit assessment of comparability, measurement, and generalizability. The status is terminated, but the reason is not reported in the registry record.

The composite result does not tell which component—myocardial infarction or congestive heart failure—contributed to the observed contrast. The timeframe is hospital length of stay, not a fixed follow-up period reported for every patient. The posted wound-infection comparison is a separate secondary result and cannot establish effects on overall morbidity or 30-day mortality, for which results are not reported in the registry record.

A p-value is not the probability that an intervention has no effect, and a confidence interval is not a guarantee about the true value. Likewise, the absence of a statistically detectable difference in a secondary outcome does not prove equivalence. The posted data do not support a claim that all benefits or harms were measured or that every relevant outcome was reported.

The registry record can support a statistical description of the recorded endpoint counts and their unadjusted contrasts. It cannot, by itself, answer questions about clinical recommendations or establish a definitive causal conclusion. The interpretation remains conditional on trial conduct, analysis choices, endpoint measurement, and reporting details that are not fully documented in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates how a randomized design and a clearly stated binary endpoint can produce a direct comparison of event counts between groups. The primary outcome is a composite, so its interpretation depends not only on the overall contrast but also on which components occurred. Since component-specific results are not reported, the composite highlights an important statistical principle: a single summary can conceal meaningful differences in the behavior of its parts.

The primary risk difference and its interval make the observed absolute-scale contrast visible, while the risk ratio and odds ratio offer relative-scale descriptions. These are complementary summaries, not interchangeable measures. Reading the estimate together with its interval is more informative than focusing on the p-value alone, because the interval conveys the range of magnitudes compatible with the data under the method used.

The contrast between the primary and secondary results also demonstrates why endpoints need to be interpreted according to their role in the study. The primary comparison has an unadjusted interval that excludes zero; the secondary wound-infection interval includes its null value. Without a reported multiplicity strategy, a hierarchy of outcomes, and complete results for the broader outcomes described in the summary, secondary findings carry less confirmatory weight.

Finally, the registry highlights the distinction between observed results and prospective planning. Sample-size illustrations based on the observed effect can show how planning requirements change for smaller assumed effects, but they do not reveal the original design rationale or the probability that the completed trial detected an effect. Clear reporting of those assumptions, along with missing-data and analysis-population methods, is essential for interpreting the strength and limits of a trial's evidence.

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 registry record does not report why the study was terminated, so the effect of termination on recruitment, follow-up, or reporting cannot be assessed. The listed enrollment and outcome denominators do not provide a participant flow, and the record does not describe exclusions, withdrawals, or missing outcome data. This makes it difficult to determine whether each analysis included all randomized participants.

The primary endpoint combines myocardial infarction and congestive heart failure, but the registry reports no component-specific counts. Event definitions, adjudication methods, and assessor masking are not reported in the registry record. Although single masking is recorded, the masked group or personnel are not identified. These gaps limit evaluation of outcome measurement and potential ascertainment bias.

The arm descriptions both state a glucose target of <150 mg/dL, but the registry does not give details of achieved glucose levels, treatment adherence, or protocol deviations. The continuous-infusion arm description specifies open peripheral vascular bypass surgery, while the intermittent-bolus description refers to peripheral vascular bypass surgery. More detailed eligibility and operative criteria are not reported in the registry record.

The primary recalculation is unadjusted, and a detailed prespecified analysis plan, primary interval method, and covariate-adjustment strategy are not reported. The registry also does not report a multiplicity plan, analysis populations, or results for overall morbidity and 30-day mortality mentioned in the study summary. These limitations constrain interpretation of the posted comparisons and the extent to which they address the broader clinical aims.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Glycemic Control to Prevent Cardiac Morbidity in Vascular Surgery — NCT00328094.
• Registry record last updated 2013-04-17; status last verified 2013-04.
• Results first posted 2013-04-09.
• 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

NCT00328094 is a randomized, single-masked, parallel-group trial sponsored by Beth Israel Deaconess Medical Center. The registry lists enrollment of 242, status as terminated, a study start of 2006-03, and primary completion of 2008-04. The reason for termination is not reported in the registry record.

The trial compared continuous intravenous insulin infusion with intermittent insulin boluses in vascular surgery. Its primary endpoint was the hospital-stay composite of myocardial infarction and congestive heart failure. The posted event counts were 4 among 114 in the continuous-infusion arm and 15 among 122 in the intermittent-bolus arm. The unadjusted recalculated risk difference was 0.088, with an interval from 0.021 to 0.155 and p = 0.013.

The posted secondary outcome was postoperative wound infection; the registry also lists safety counts and hypoglycemia as the top serious adverse event term. Detailed analysis plans, missing-data methods, component-specific primary results, and results for overall morbidity and 30-day mortality are not reported in the registry record.