Effect of Lantus and Apidra in Patients With Acute ST Elevation Myocardial Infarction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Lantus and Apidra in Patients With Acute ST Elevation Myocardial Infarction (NCT00670228), a randomized phase 3 study. The primary outcome is Infarct Size Absolute Change From Baseline at Day 60.

2. Clinical Question

The registry describes a trial intended to evaluate whether tight glycemic control with insulin glulisine and insulin glargine could reduce infarct size in this specific clinical setting. The question is about a measured change in cardiac imaging, not a direct comparison of symptoms, survival, or every possible cardiovascular outcome. The brief summary also identifies inflammation, left ventricular function, and cardiovascular outcomes as secondary interests.

The posted primary results are group means and a mean difference for the modified intention-to-treat population. They therefore address the average observed change among participants meeting that endpoint population definition. They do not describe the experience of every randomized participant, because the primary analysis required medication exposure, PCI, and a valid post-PCI infarct-size result.

3. Trial Design

The registry identifies this as a randomized, parallel-group, multicenter phase 3b clinical trial. The official title describes it as stratified and open-label; the registry lists no masking. Participants were assigned to intensive insulin therapy or standard glycemic care. Because treatment assignment was not masked, participants and clinical staff could know which care strategy was being used. The registry does not report further detail about the stratification procedure or allocation implementation.

The intensive regimen combined intravenous insulin glulisine with subcutaneous insulin glargine and targeted blood glucose between 90-130 mg/dL. Standard glycemic care used subcutaneous regular insulin per sliding scale. These are treatment strategies rather than identical interventions differing only in one insulin product, so the comparison concerns the assigned care approaches as described in the record.

Enrollment was 34. The registry gives a trial start of 2008-04 and primary completion of 2009-11, and lists the status as terminated. A reason for termination is not reported in the registry record. The record names Sanofi as sponsor. It does not report the original sample-size justification, the recruitment target rationale, or the planned analysis details beyond the outcome descriptions and the population definition.

Four outcome measures are listed, including the primary infarct-size measure and secondary measures of left ventricular function, major adverse cardiovascular events, and C-reactive protein. Three secondary outcomes have numerical results posted, while a numerical MACE result is not reported in the registry record. A termination status and a small enrollment are important context for interpreting the limited amount of outcome information, but neither alone explains why results are incomplete.

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: Although 34 patients signed the informed consent form for study inclusion, one patient did not sign the Health Insurance Portability and Accountability Act (HIPAA) form, electing to keep his/her medical information private, and was therefore not randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on the Modified Intention To Treat (MITT) population which includes all randomized subjects who took at least one dose of the study medication, undergone PCI procedure at hospital admission, and had a valid post-PCI infarct size.

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 Infarct Size Absolute Change From Baseline at Day 60, measured over From baseline at Day 60.

The primary endpoint is the absolute change in infarct size from baseline at day 60, measured as a percentage of left ventricular mass by cardiac magnetic resonance imaging. MRI provides an imaging-based measure of the portion of the left ventricle identified as infarcted. Expressing infarct size relative to left ventricular mass makes the endpoint a continuous measure rather than a simple event count.

Change from baseline is intended to describe how the measured endpoint differs between the baseline assessment and the day-60 assessment. The registry identifies the endpoint as a mean and reports standard deviations for each arm. The result therefore summarizes the average change in each analyzed group, while the standard deviation describes the spread of individual observations around each group mean. The registry does not specify the sign convention used to calculate change, so the direction of a negative value should be read in conjunction with that convention, which is not reported in the registry record.

Infarct size was chosen as the primary measure because the stated primary objective was to compare infarct size at day 60 between the two glycemic-care approaches in hyperglycemic subjects with anterior STEMI undergoing PCI. It is an imaging endpoint, not itself a direct measure of how a participant feels or functions. Its relevance to other clinical outcomes would require evidence beyond the group means posted for this endpoint.

The primary analysis used a modified intention-to-treat population. The definition includes randomized subjects who took at least one study dose, underwent PCI at hospital admission, and had a valid post-PCI infarct-size measurement. The registry does not provide a participant-level flow explaining who did or did not meet each condition.

7. Results Posted in the Registry

• Intensive Insulin Therapy (IIT): mean -7.84 versus -15.72 on control; difference 7.88 (95% CI -5.91 to 21.67), standardized effect d = 0.45; z-test p = 0.263.

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.

Left Ventricular (LV) Function Evaluated by Cardiac Magnetic Resonance Imaging (MRI)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Intensive Insulin Therapy (IIT): mean 43.08 versus 43.43 on control; difference -0.35 (95% CI -8.10 to 7.40), standardized effect d = -0.04; z-test p = 0.929.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intensive Insulin Therapy (IIT) and the control. The interval gives the range of effects that remain compatible with the data.

Biomarkers of Inflammation Measurement: CRP (C-Reactive Protein)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Intensive Insulin Therapy (IIT): mean 2.52 versus 2.96 on control; difference -0.44 (95% CI -3.06 to 2.18), standardized effect d = -0.13; z-test p = 0.742.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intensive Insulin Therapy (IIT) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover left ventricular ejection fraction at day 3 and C-reactive protein at day 60, alongside a listed outcome for major adverse cardiovascular events. Numerical summaries and unadjusted comparisons are posted for the first two. A numerical result for MACE is not reported in the registry record. Taken together, the posted secondary results do not provide a consistent, precise body of evidence that resolves the uncertainty in the primary infarct-size comparison.

Secondary endpoints address different dimensions of the clinical question. Left ventricular function is an imaging measure of cardiac function, while C-reactive protein is an inflammation biomarker. Neither measures infarct size in the same way as the primary endpoint. Agreement across different kinds of outcomes could contribute context, but a secondary measure cannot replace the prespecified primary endpoint or establish that an imaging difference translates into a patient-important outcome.

General statistical explanation: secondary outcomes often have less evidential weight than the primary outcome because they may be numerous, may be tested without adjustment, and may not have been the main basis for trial planning. When several endpoints are considered, chance can produce apparently notable findings. Their interpretation depends on whether hypotheses and analysis methods were prespecified, how missing values were handled, and whether multiplicity was controlled. Those details are not reported in the registry record.

The secondary findings should therefore be read as descriptive and exploratory unless a fuller analysis plan establishes otherwise. They may help identify questions for further study, but the posted record does not show a multiplicity-adjusted analysis or a complete inferential framework. The overall pattern does not overcome the small primary analysis population, the wide primary interval, or the absence of detailed analysis methods. This does not mean that the secondary outcomes are uninformative; it means their role in drawing a confirmatory conclusion is limited by the available documentation.

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

• Left Ventricular (LV) Function Evaluated by Cardiac Magnetic Resonance Imaging (MRI)
• Occurrence of the Major Adverse Cardiovascular Events (MACE)
• Biomarkers of Inflammation Measurement: CRP (C-Reactive Protein)

9. Statistical Interpretation

10. Statistical Methods Explained

Understanding the results starts with the distinction between a group summary and a treatment comparison. The arm means describe the average observed endpoint change within each analyzed group. The mean difference compares those averages, with the registry’s comparison defined as intensive insulin therapy versus standard glycemic care. A positive or negative contrast depends on that ordering and on the endpoint’s sign convention; the latter is not reported in the registry record.

What does the standard deviation describe?

The standard deviation describes how spread out participant measurements are around the mean within an arm. It is not the uncertainty in the mean difference itself, and it is not a range containing all participants. A large standard deviation indicates substantial variation among observations relative to the mean. In this trial, the posted standard deviations for infarct-size change are 9.19 and 22.41. Those summaries show that the observed variability was not identical across the two arms.

General statistical explanation: the standard error describes the estimated sampling variability of a statistic, such as a mean or mean difference. It depends on both the variability of observations and the amount of information in the sample. Small samples generally yield less precise estimates than larger samples when other features are similar. Individual-level data are not posted, so the distributions, outliers, and influence of particular observations cannot be examined from the registry summaries.

How should the confidence interval be read?

The primary mean-difference interval runs from -5.914 to 21.67 around an estimate of 7.88. General statistical explanation: a confidence interval is a range of values generated by a procedure that reflects uncertainty in an estimate under the assumptions used. It is not a guarantee that the true effect lies in the interval, nor does it assign probabilities to individual values after the interval has been calculated. The confidence level and exact method used for the registry’s interval are not reported in the registry record.

The interval includes zero, which represents no difference in group means on the contrast scale. It also includes values below and above zero. This means the data do not sharply distinguish among several possible contrasts. The interval’s width matters: it indicates that the estimate is not precise enough to rule out a range of potentially meaningful differences. The record does not state what difference would be clinically important, so statistical uncertainty cannot be converted into a judgment about clinical importance.

What does the p-value add?

The reported p-value for the primary comparison is 0.263 and is labeled unadjusted. General statistical explanation: a p-value measures how surprising data at least as incompatible with a null hypothesis as the observed data would be, assuming that null hypothesis and the statistical model are correct. It is not the probability that the null hypothesis is true, nor does it tell how likely a replication is to produce the same estimate. It also does not measure effect magnitude. Here, the p-value should be read alongside the estimate, interval, sample sizes, endpoint definition, and missing analysis details.

The registry does not report a formal sponsor analysis for the primary comparison. The displayed comparison is a simple unadjusted recalculation from posted summary statistics. The discrepancy indicator is false, so there is no listed conflict between a posted sponsor estimate and that recalculation. Even so, a recalculated summary is not a substitute for a complete prespecified analysis with its model, covariates, handling of missing data, and sensitivity analyses documented.

Why does over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variation is greater than a statistical model expects. It can make standard errors too small if the model assumes less variability than the data contain, leading to intervals that are too narrow and tests that appear more decisive than warranted. For a continuous endpoint, unequal arm variability is a related concern when methods assume a common variance. The posted standard deviations differ, but the registry does not identify the inferential method or provide the individual data needed to evaluate model fit. It would therefore be inappropriate to claim that over-dispersion occurred or that any particular correction was used.

Randomization aims to make treatment groups comparable on average, but it does not guarantee balance in a small realized sample. The posted sample sizes are 11 and 12 for the primary endpoint. With such limited information, baseline characteristics or prognostic factors may differ by chance, and chance imbalance can affect an unadjusted comparison. Baseline infarct-size values and a detailed baseline balance assessment are not reported in the registry record.

The analysis population also affects interpretation. Modified intention-to-treat is not identical to an analysis of all randomized participants: eligibility for this endpoint required medication exposure, PCI, and a valid post-PCI infarct-size measurement. That definition is explicit, but the record does not give reasons for exclusion or a comparison of included and excluded participants. If inclusion depends on participant characteristics or outcomes, the resulting estimate could differ from the effect among all randomized participants. The registry summaries do not allow that possibility to be assessed.

Finally, inferential results are described as unadjusted. The registry does not report a multiplicity strategy, adjustment for baseline variables, or a detailed statistical analysis plan. General statistical explanation: when several outcomes or comparisons are examined, the chance of at least one apparently notable result can increase unless the analysis accounts for the number and structure of tests. This concern is especially relevant when secondary outcomes are interpreted as confirmatory rather than exploratory. The record provides too little information to determine what testing strategy was originally planned.

11. Confidence Intervals and Precision

The primary mean difference is 7.88, and its confidence interval extends from -5.914 to 21.67. Because the interval includes zero and reaches both negative and positive values, the estimate does not pin down a single direction of difference. It is compatible with an average contrast below zero, no difference, or a contrast above zero under the interval’s assumptions. The interval is also wide relative to the point estimate, reflecting limited precision.

Precision is distinct from whether a result crosses a statistical significance threshold. The unadjusted p-value is 0.263, but the interval offers a more direct view of the range of contrasts compatible with the data under the method used. The registry does not report the interval’s confidence level or construction method, so those features cannot be independently evaluated from the record.

The small analyzed groups, 11 and 12 participants, and the standard deviations of 9.19 and 22.41 provide context for the uncertainty. General statistical explanation: an estimate based on few observations will often be sensitive to individual values, particularly when measurements vary substantially. The registry’s arm-level summaries cannot show whether the means were influenced by outliers or by a skewed distribution.

The interval does not establish that the two care strategies are equivalent. Equivalence requires a prespecified range of differences considered acceptably small and an interval sufficiently contained within that range. Such a margin is not reported in the registry record. Likewise, the interval cannot identify clinical importance without a stated threshold for an important difference. It supports a cautious reading: the mean contrast is estimated with substantial uncertainty, and effects in more than one direction remain compatible with the posted result.

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, not total participants, for this continuous outcome. They are illustrations based on the observed effect rather than the trial’s original design assumptions. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm under those planning assumptions for a design with an 80% chance of detecting the specified effect if that effect is real and the assumptions hold. The 90% power column gives the corresponding per-arm planning amount for a 90% chance under the same framework. These are prospective design calculations, not descriptions of the enrolled or analyzed groups.

Rows that plan for 75% or 50% of the observed effect represent smaller target differences than planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under the stated assumptions. The figures can change substantially with the assumed effect size and with departures from the planning model, including unequal allocation, non-normal data, or a different analysis plan.

These figures are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the result’s estimate and confidence interval: the posted interval already conveys the uncertainty in the estimated contrast more directly. The registry does not report whether these illustrations correspond to the sponsor’s original plan; they are explicitly calculated from the observed effect.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 7.880; pooled standard deviation σ = 17.415.
2. n = 2 × (1.96 + 0.842)² × 17.415² / 7.880² = 76.7, rounded up to 77 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 <- 7.88                      # observed difference in means
sigma <- 17.4148952391473                     # 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(670228)
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 = 77 (80% power), 103 (90% power)
 75% of observed effect: n per arm = 137 (80% power), 183 (90% power)
 50% of observed effect: n per arm = 307 (80% power), 411 (90% power)
power.t.test: 77.6 
Simulated power at n = 77 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, treatment contrasts, or subgroups. If each is tested separately without accounting for the number of tests, the chance of at least one false-positive result can increase. This is a general statistical concern, not a claim that a particular false-positive finding occurred in this trial. The registry lists a primary endpoint and several secondary outcome areas, but a multiplicity adjustment strategy is not reported in the registry record.

The record does not report a complete statistical analysis plan, the hierarchy of secondary hypotheses, or whether any secondary tests were intended to be confirmatory. It also does not report interim analyses or stopping rules. These details should not be inferred from the trial’s terminated status. The reason for termination and any relationship between termination and the results are not reported in the registry record.

The primary endpoint population is defined as modified intention-to-treat: randomized participants who took at least one dose, underwent PCI at hospital admission, and had a valid post-PCI infarct-size measurement. That definition clarifies who was analyzed for the endpoint, but a participant-flow account is not reported. The registry does not show how many randomized participants failed each condition or why measurements were unavailable. It also does not describe methods for handling missing data or sensitivity analyses to assess their potential effect.

Because the endpoint analysis excludes participants without the required measurement and treatment exposure, its estimate applies directly to the defined analysis population. Whether it generalizes to all randomized participants depends in part on why some participants were not included. The record does not permit an assessment of whether missingness was related to prognosis, treatment assignment, or outcome values.

Baseline adjustment, covariate selection, model diagnostics, and the inferential method for the primary comparison are not reported in the registry record. Nor are the original sample-size justification and assumptions. These omissions limit reproducibility and make it difficult to determine how closely the posted summaries reflect the intended analysis. The registry results remain useful as descriptive evidence, but should not be treated as a full substitute for a detailed clinical study report.

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: ventricular tachycardia (15.4%), bradycardia (12.5%), hypotension (12.5%), cardiac failure congestive (7.7%), cardiogenic shock (7.7%).

The registry reports serious adverse events among 16 participants at risk in intensive insulin therapy and 13 at risk in standard glycemic care. The number affected by serious adverse events was 6 in the intensive arm and 3 in the standard-care arm. Other, non-serious adverse events affected 10 and 6 participants, respectively, using those same arm-specific at-risk counts. These counts describe the participants recorded as affected; they do not establish that the treatment caused the events.

The listed serious-event terms include ventricular tachycardia at 15.4%, bradycardia at 12.5%, hypotension at 12.5%, cardiac failure congestive at 7.7%, cardiogenic shock at 7.7%, and pericardial effusion at 6.2%. The registry does not provide enough information in these summaries to determine event timing, severity beyond the serious-event classification, recurrence, or attribution to treatment. The percentages should be read as registry-reported term frequencies, not as comparative risk estimates.

Deaths are not reported in the registry record; a blank death field should not be interpreted as evidence that no deaths occurred. The small groups and absence of detailed event-level information limit comparisons between arms. These safety counts are descriptive and do not, on their own, establish a causal difference in adverse-event risk.

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

The posted primary result is a mean change comparison from a small modified intention-to-treat population. The intensive insulin therapy group had a mean change of -7.84, and standard glycemic care had a mean change of -15.72. The reported difference was 7.88, with a confidence interval from -5.914 to 21.67 and an unadjusted p-value of 0.263. The interval includes zero and is broad, so the estimate does not settle whether the underlying average contrast is positive, negative, or absent.

This result does not establish that the strategies are equivalent, nor does it establish superiority of either approach. A nonsignificant p-value is not proof of no effect. A superiority claim would require an adequately precise estimate and an analysis aligned with the trial’s design. An equivalence or noninferiority claim would also require a prespecified margin, which is not reported in the registry record.

The endpoint is an MRI measure of infarct size as a percentage of left ventricular mass, not a direct report of symptoms, quality of life, or survival. The brief summary identifies other clinical and biological outcomes, but the posted secondary results do not provide a complete assessment of all those outcomes. In particular, a numerical MACE result is not reported in the registry record. It is therefore not appropriate to extend the primary imaging result into a broad statement about cardiovascular outcomes.

The trial’s enrollment was 34, while the primary outcome arm sizes were 11 and 12. The record does not provide a full account of participant inclusion and exclusion for the analysis. It also lists the trial as terminated without reporting why. Those features limit certainty about the scope and completeness of the evidence, but do not by themselves explain the observed result.

The appropriate conclusion is narrow: the registry posts an uncertain comparison of mean infarct-size changes in the defined analysis population. It does not provide enough precision or methodological detail to support a definitive interpretation of the treatment contrast, and it does not answer every clinical question raised by the trial’s objectives.

17. Why This Trial Matters Statistically

This trial illustrates why the numerical estimate, uncertainty, and analysis population need to be considered together. A group mean difference alone can appear clear-cut, but the confidence interval shows how much uncertainty surrounds that estimate. Here, the primary interval spans values below and above zero, while the analyzed groups are small. Reading only the point estimate or p-value would miss important information about precision.

It also demonstrates that randomized assignment does not eliminate uncertainty in a small trial. Randomization supports a fair comparison in expectation, but the realized groups can still differ by chance, and small samples provide limited ability to average out individual variation. The reported standard deviations show meaningful spread in the primary measure, reinforcing the need to avoid over-reading the group means.

The modified intention-to-treat definition is another key statistical issue. It specifies the participants included in the endpoint analysis, but it is narrower than all randomized participants. Without participant flow and reasons for missing endpoint data, readers cannot assess the potential consequences of exclusion or determine how representative the analysis is of the randomized population.

Finally, a registry record can contain outcome summaries without documenting every element needed to reproduce or evaluate the inferential analysis. The absence of a detailed analysis plan, sample-size justification, multiplicity approach, and missing-data methods limits the strength of conclusions that can be drawn. These are not merely administrative details: they determine which population, estimand, and uncertainty calculation the results represent.

The statistical lesson is to distinguish a descriptive result from a decisive finding. The posted numbers provide useful information about what was observed, but precision, completeness, and design context determine how far that information can reasonably be interpreted.

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 main limitation is the small number of participants contributing to the primary endpoint: 11 in intensive insulin therapy and 12 in standard glycemic care. With these group sizes, the estimate may be sensitive to individual measurements, and the interval is broad. The registry does not post participant-level data, so the effects of outliers, skewness, or other distributional features cannot be assessed.

The analysis population requires exposure to study medication, PCI at admission, and a valid post-PCI infarct-size measurement. The record does not provide a complete flow from randomization through endpoint analysis or explain why participants were not included. This prevents evaluation of potential selection effects and limits comparison between the analyzed participants and all randomized participants.

The trial was open-label, and no masking is listed. The primary outcome is based on cardiac MRI, but the registry does not describe image-reading procedures, reader masking, or quality control. These details are not reported in the registry record and should not be presumed. The registry also does not describe allocation concealment, stratification factors, baseline balance, or any adjusted analysis.

The trial is listed as terminated, but the reason is not reported. The record does not provide the original sample-size justification, a full statistical analysis plan, multiplicity handling, interim-analysis plans, or missing-data methods. A numerical MACE result is also not reported. Together, these omissions restrict assessment of the completeness and confirmatory status of the posted outcomes.

These limitations do not show that the results are biased or invalid; they identify questions that the registry summaries cannot resolve. More complete trial documentation would be needed to evaluate the analysis choices and the potential influence of missing data, protocol deviations, or outcome measurement procedures.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effect of Lantus and Apidra in Patients With Acute ST Elevation Myocardial Infarction — NCT00670228.
• Registry record last updated 2011-02-11; status last verified 2011-01.
• Results first posted 2011-02-11.
• 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

The registry describes a randomized, parallel-group, open-label phase 3b trial comparing intensive insulin therapy with standard glycemic care in hyperglycemic subjects with anterior STEMI undergoing PCI. Enrollment was 34, and the status is terminated. The primary outcome was change in MRI-measured infarct size from baseline at day 60, analyzed in a modified intention-to-treat population.

The posted primary mean difference was 7.88, with a confidence interval from -5.914 to 21.67 and an unadjusted p-value of 0.263. The small endpoint groups and wide interval limit precision. Secondary numerical results are posted for left ventricular ejection fraction and C-reactive protein; a numerical MACE result is not reported in the registry record.

The registry does not report the reason for termination, the original sample-size justification, a full statistical analysis plan, multiplicity handling, or missing-data methods. The results are best read as limited descriptive and inferential information rather than a definitive resolution of the treatment comparison.