Efficacy and Safety of Lixisenatide Versus Placebo on Top of Basal Insulin and/or Oral Antidiabetic Treatment in Older Type 2 Diabetic Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Lixisenatide Versus Placebo on Top of Basal Insulin and/or Oral Antidiabetic Treatment in Older Type 2 Diabetic Patients (NCT01798706), a randomized phase 3 study. The primary outcome is Absolute Change in HbA1c From Baseline to Week 24.

2. Clinical Question

3. Trial Design

This was a randomized, phase 3, double-blind, placebo-controlled, parallel-group, multicenter study. The registry lists quadruple masking. The study assessed lixisenatide safety and efficacy over 24 weeks in older patients with type 2 diabetes inadequately controlled on their current treatment. The registry lists enrollment as 350.

The treatment groups received lixisenatide or matched placebo, with antidiabetic background therapy. Lixisenatide was administered once daily, starting at 10 mcg for 2 weeks and then at a maintenance dose of 20 mcg through Week 24; the dose could be reduced to 10 mcg if 20 mcg was not tolerated. Placebo was administered once daily for 24 weeks.

The primary objective was to evaluate the effect of lixisenatide versus placebo on HbA1c reduction over 24 weeks. The principal secondary objective concerned safety and tolerability, including documented symptomatic hypoglycemia and gastrointestinal side effects. Other listed objectives included fasting plasma glucose, glucose measures following a standardized breakfast challenge, self-monitored glucose profiles, body weight, basal insulin dose where applicable, rescue therapy, pharmacokinetics, and antibody development.

The primary efficacy analysis used the modified intent-to-treat population. That definition included randomized participants who received at least one dose and had both baseline and at least one post-baseline efficacy assessment, regardless of compliance with study procedures. The registry record does not report the original sample-size justification or the detailed procedures used to implement masking.

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: A total of 426 participants underwent 4 week placebo run-in period. 436 participants were screen failures and 76 were run-in failures; the most frequent reason for screen and run-in failure was glycosylated hemoglobin (HbA1c) criteria not met at end of the run-in phase. A total of 350 participants were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent to treat (mITT) population: all randomized participants who received at least one dose of study drug; and had both baseline and at least one post-baseline efficacy assessment, irrespective of compliance with study protocol/procedures.

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 Absolute Change in HbA1c From Baseline to Week 24, measured over Baseline, Week 24.

The primary endpoint was absolute change in HbA1c from baseline to Week 24, measured as a percentage of hemoglobin. Change was defined as the Week 24 value minus the baseline value. HbA1c reflects average blood glucose over time and is commonly used in clinical research as a measure of longer-term glycemic control; this is general context about the measure, not an additional finding from this trial.

The endpoint compares the average change in each treatment group, with the main contrast being the difference between those changes. A more negative change represents a larger reduction from baseline. In the posted results, the lixisenatide group’s least-squares mean change was -0.57 and the placebo group’s was 0.06. The sponsor-reported adjusted comparison was a least-squares mean difference of -0.64.

Missing primary endpoint data were imputed using last on-treatment observation carried forward (LOCF). The on-treatment period was defined as the time from the first study-drug dose through 14 days after the last dose. Participants counted in the primary analysis had a baseline assessment and at least one post-baseline HbA1c assessment during that period. The endpoint therefore represents the specified analysis and imputation approach, rather than a measurement available for every randomized participant at Week 24.

7. Results Posted in the Registry

• Lixisenatide: mean -0.57 versus 0.06 on control; difference -0.63 (95% CI -0.83 to -0.43), standardized effect d = -0.65; z-test p = <0.001.

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.

Change in 2-Hour PPG From Baseline to Week 24

• 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 errors.
• Result:
  • Lixisenatide: mean -5.12 versus -0.07 on control; difference -5.05 (95% CI -6.14 to -3.96), standardized effect d = -1.07; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Lixisenatide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Average 7-point SMPG Profiles From Baseline to Week 24

• 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 errors.
• Result:
  • Lixisenatide: mean -1.15 versus -0.19 on control; difference -0.96 (95% CI -1.48 to -0.44), standardized effect d = -0.45; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Lixisenatide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Body Weight From Baseline to Week 24

• 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 errors.
• Result:
  • Lixisenatide: mean -1.47 versus -0.16 on control; difference -1.31 (95% CI -1.96 to -0.66), standardized effect d = -0.42; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Lixisenatide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary results broadly follow the direction of the primary HbA1c finding. The posted glucose-related outcomes show larger average reductions in the lixisenatide group than in the placebo group, while the body-weight outcome also shows a larger average decrease in the lixisenatide group. These patterns provide context across related outcomes, but they do not replace the primary endpoint or establish effects beyond the measured outcomes and period.

The secondary measures address different aspects of glucose control and treatment experience, including post-meal glucose, self-monitored profiles, fasting glucose, glucose excursions, basal insulin dose, rescue therapy, and hypoglycemia. Ten secondary outcomes are posted, while the registry lists a broader set of planned secondary outcome measures. Results for every listed secondary measure are not available in the posted secondary results summarized in the registry record.

Unadjusted secondary p-values carry less weight when many outcomes are examined. In general, conducting multiple tests increases the chance that some results may appear statistically notable even when no corresponding effect exists. A multiplicity procedure can address that issue, but the registry record does not report an adjustment for multiplicity or a hierarchy governing the secondary tests. Secondary findings are therefore best read as supportive or exploratory, rather than as a set of independent confirmatory conclusions.

Consistent directions across related measures can strengthen the descriptive coherence of the results, but the outcomes may be correlated and do not constitute independent replications. The registry record does not report enough detail to assess all secondary analysis populations, missing-data procedures, or adjustment choices.

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

• Change in 2-Hour PPG From Baseline to Week 24
• Change in Average 7-point SMPG Profiles From Baseline to Week 24
• Change in Body Weight From Baseline to Week 24
• Change in FPG From Baseline to Week 24
• Percentage of Participants Requiring Rescue Therapy During 24 Week Treatment Period
• Change in Plasma Glucose Excursions From Baseline to Week 24
• Change in Total Daily Basal Insulin Dose From Baseline to Week 24 (in Participants Who Took Basal Insulin as Background Therapy)
• Percentage of Participants With Symptomatic and Severe Symptomatic Hypoglycemia

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: HbA1c change is measured on a numeric scale, and the registry reports least-squares means with standard errors. A mean summarizes the central tendency of a continuous outcome. A standard error describes the statistical uncertainty around an estimated mean; it is not the same thing as the spread of individual participant measurements. This distinction is general statistical context.

What does the ANCOVA estimate represent?

The registry reports an analysis of covariance (ANCOVA), with a least-squares mean difference between lixisenatide and placebo. In general, ANCOVA compares groups while accounting for specified covariates in a statistical model. The resulting least-squares means are model-based adjusted estimates rather than simply the raw arithmetic averages. The registry record does not identify the covariates used in this ANCOVA, so their identities should not be inferred.

The sponsor-reported difference is -0.64, with a 95% confidence interval from -0.81 to -0.464 and p < 0.001. The negative sign indicates that the estimated change is lower in the lixisenatide group than in the placebo group, consistent with a greater mean reduction from baseline. The reported interval and p-value arise from the sponsor’s analysis, not the separate unadjusted re-calculation.

What is the re-calculation?

The re-calculated comparison uses the posted group means and standard errors to form a simple unadjusted group contrast. It estimates a mean difference of -0.63, and the unadjusted p-value is <0.001. The standard deviations used for this re-calculation are approximated from the reported standard errors and group sizes. This is a summary-statistic calculation, not a reconstruction of the sponsor’s ANCOVA. The registry reports no discrepancy flag; in any event, the sponsor’s own analysis is the relevant reported analysis when interpreting the trial’s primary result.

The re-calculation is useful as a transparent check on the scale and direction of the comparison. It cannot reproduce covariate adjustment, participant-level data handling, or model details that are not available in the registry record. A close numerical result does not make the methods interchangeable.

How should the p-value be understood?

In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. A small p-value is not a measure of clinical importance, does not show the probability that a result occurred “by chance,” and does not quantify the chance that the finding will replicate. Interpretation should also consider the estimated difference and its confidence interval.

The registry includes a 95% confidence interval for the sponsor analysis. In general, a confidence interval expresses the uncertainty of an estimate under the statistical procedure used: intervals generated repeatedly by that procedure would cover the true parameter at the stated rate if the model assumptions hold. It does not mean there is a 95% probability that this particular fixed interval contains the true effect.

The outcome’s missing values were handled using LOCF for the primary efficacy variable. This method carries forward the last on-treatment observation for a participant with later missing measurements. It creates an analysis value but does not turn an unobserved Week 24 measurement into an observed one. The registry record does not report sensitivity analyses testing alternative missing-data assumptions.

General statistical caution: estimates and tests depend on the analysis population, model, measurement process, and missing-data approach. The trial’s registered primary population required at least one post-baseline efficacy assessment, so it was not simply every randomized participant. Details beyond the stated population definition and LOCF procedure are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s primary comparison is reported as a least-squares mean difference of -0.64, with a 95% confidence interval from -0.81 to -0.464. The interval is entirely below zero, so the reported analysis is compatible with a negative group difference across the interval’s bounds. In context, negative values correspond to a greater mean reduction in HbA1c for lixisenatide than for placebo.

A confidence interval gives a range of estimates reasonably compatible with the observed data and the statistical procedure, under its assumptions. Its width conveys precision: a narrower interval indicates less statistical uncertainty about the estimated contrast, while a wider interval indicates more. The interval does not show the range of individual participant responses, and it does not guarantee that the true effect falls inside the particular interval.

The registry also reports a standard error for each group least-squares mean: 0.075 for lixisenatide and 0.072 for placebo. These standard errors describe uncertainty around the group estimates, rather than the variability of individual HbA1c values. The sponsor’s adjusted interval should be preferred for interpreting the sponsor’s ANCOVA result. The unadjusted re-calculation is based on summary statistics and is a separate analysis.

Precision is distinct from importance. The interval and p-value address statistical uncertainty under the model; they do not determine whether the difference is meaningful to patients, establish persistence beyond Week 24, or describe how consistently individuals respond. The registry record does not report a threshold for interpreting the clinical importance of an HbA1c difference.

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 event counts. They are illustrations based on the observed effect, using a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning row considers an effect equal to the stated fraction of the observed effect. These are planning illustrations, not observed power.

The 80% power column gives the estimated number of participants per arm for a design intended to have an 80% chance of detecting the specified effect at the stated significance level, assuming the planning model and effect are correct. The 90% power column uses a higher target chance of detecting that effect and therefore generally calls for more participants per arm. These concepts describe prospective design properties, not the probability that the trial’s result is true.

Rows for 100%, 75%, and 50% of the observed effect illustrate how the required per-arm sample size changes when the effect a future study aims to detect is smaller than the observed estimate. Smaller effects need more participants to distinguish them from random variation at a given power target and significance level. The calculations are not the trial’s original design justification. The original design assumptions and sample-size justification are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.630; pooled standard deviation σ = 0.964.
2. n = 2 × (1.96 + 0.842)² × 0.964² / -0.630² = 36.8, rounded up to 37 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.63                      # observed difference in means
sigma <- 0.964144180089264                     # 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(1798706)
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 = 37 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 66 (80% power), 88 (90% power)
 50% of observed effect: n per arm = 148 (80% power), 197 (90% power)
power.t.test: 37.8 
Simulated power at n = 37 per arm: 0.793 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as ANCOVA, with a least-squares mean difference of -0.64, a 95% confidence interval from -0.81 to -0.464, and p < 0.001. This is an adjusted analysis. The simple re-calculation from posted group summary statistics estimates an unadjusted mean difference of -0.63, with p <0.001.

The estimates are close in direction and magnitude, but the re-calculation does not reproduce the sponsor’s ANCOVA. It uses summary statistics and does not account for any model covariates. The registry does not report which covariates the ANCOVA included. The sponsor’s analysis is therefore the principal result for the trial’s primary endpoint; the re-calculation is a supplementary check, not a replacement.

The registry record does not flag a discrepancy between the re-calculation and the reported analysis. Differences in method and adjustment still matter when comparing the two estimates. The confidence interval and p-value reported by the sponsor should be interpreted as belonging to the ANCOVA result.

15. Multiplicity, Missing Data and Analysis Populations

The primary efficacy population was the modified intent-to-treat population: randomized participants who received at least one dose of study drug and had both baseline and at least one post-baseline efficacy assessment, irrespective of compliance with protocol or procedures. The registry record describes this population and reports the analyzed group sizes for the primary outcome.

For the primary HbA1c outcome, missing data were imputed using last on-treatment observation carried forward. The on-treatment period ran from the first dose through 14 days after the last dose. This defines how the primary analysis treated missing measurements; it does not establish that the imputation assumptions are correct. The registry record does not report sensitivity analyses using alternative missing-data methods.

Multiple secondary outcomes were assessed. In general, the more statistical tests performed, the greater the chance of at least one false-positive finding if all are interpreted at the same unadjusted threshold. The registry record does not report a multiplicity adjustment, a testing hierarchy for the secondary outcomes, or whether secondary analyses were designated confirmatory or exploratory. The unadjusted secondary p-values should therefore be interpreted cautiously.

The registry record does not report the original sample-size justification, interim analyses, or the full statistical analysis plan. It also does not provide the ANCOVA covariates in the posted primary analysis description. These omissions limit the ability to evaluate all planned analysis choices and their relationship to the results.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: bronchitis (0.6%), cerebrovascular accident (0.6%), epilepsy (0.6%), loss of consciousness (0.6%), transient ischaemic attack (0.6%).

The registry reports serious adverse events in 8 of 176 participants at risk in the lixisenatide group and 10 of 174 in the placebo group. These are counts of participants with serious adverse events in the registry’s safety reporting, not a comparison adjusted for follow-up time or other factors. The registry lists several serious adverse event terms at 0.6% each: bronchitis, cerebrovascular accident, epilepsy, loss of consciousness, transient ischaemic attack, and acute myocardial infarction.

For other adverse events, the registry reports 89 of 176 participants at risk in the lixisenatide group and 58 of 174 in the placebo group. These figures refer to the registry’s “other” adverse-event category and should not be conflated with serious adverse events. The registry does not report death counts in this record.

These counts are descriptive. They do not by themselves establish whether an event was caused by study treatment, and they do not capture event severity, duration, or individual clinical context beyond the registry’s categorization. The registry record’s primary safety objective included tolerability, documented symptomatic hypoglycemia, and gastrointestinal side effects; interpretation of the listed figures should remain limited to the event categories and counts reported.

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

The primary result indicates that, in the trial’s modified intent-to-treat analysis over 24 weeks, the average HbA1c change was more negative with lixisenatide than with placebo. The sponsor-reported adjusted difference and its confidence interval support a group-level difference under the stated analysis. The posted secondary outcomes generally offer directionally consistent context across glucose measures, with a larger average body-weight decrease also reported for lixisenatide.

This is not evidence that every participant experienced the average change, nor does a group mean describe the range of individual responses. A statistically clear group comparison is not, by itself, a judgment about clinical importance. The registry record does not state a threshold for clinically important HbA1c change, and it does not support conclusions about an individual’s likely response.

The trial assessed outcomes through Week 24. The results do not establish what happens after that period, and they cannot answer questions about outcomes that were not reported. The registry record also does not give enough information to assess every aspect of the statistical plan, including the original sample-size justification, the full ANCOVA specification, and sensitivity analyses for missing data.

Safety findings should be read as descriptive event counts, not proof of causation or a complete account of risk. The registry’s adverse-event figures alone cannot establish that one treatment is safer or less safe overall. The findings apply to the trial population and analysis definitions; generalization to other populations or treatment circumstances requires evidence beyond these registry results.

18. Why This Trial Matters Statistically

This trial illustrates why a primary endpoint, analysis population, and missing-data rule matter when interpreting a clinical comparison. The primary outcome is clearly defined as change in HbA1c from baseline to Week 24, and the registry states how missing values were handled using LOCF. Those details help readers understand what quantity the reported estimate represents.

It also shows the distinction between a model-based sponsor analysis and an unadjusted re-calculation. The sponsor’s ANCOVA result is the registered primary comparison; a calculation from group summary statistics can check the general direction and scale but cannot recreate the covariate-adjusted model. Keeping those analyses distinct prevents a useful numerical check from being mistaken for the trial’s main analysis.

Finally, the trial includes a range of secondary glucose, body-weight, and safety outcomes. Such outcomes can add context, while also raising the statistical issue of multiple testing. Without a reported multiplicity strategy, secondary p-values do not have the same confirmatory standing as the primary analysis. This is a practical example of why effect estimates, uncertainty, endpoint hierarchy, and analysis transparency should be considered together.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification or the assumptions used to plan the trial. The planning illustrations based on observed effects should not be read as a description of the trial’s original design.

The primary missing-data method was LOCF, but the registry record does not report sensitivity analyses using alternative assumptions. It also does not report the covariates included in the sponsor’s ANCOVA, limiting independent evaluation of the adjustment. The unadjusted re-calculation uses summary statistics and approximate standard deviations, so it cannot reproduce participant-level modeling or missing-data handling.

Ten secondary outcomes are posted, and the registry record does not report a multiplicity adjustment or testing hierarchy. This makes secondary p-values less conclusive when considered across many outcomes. Results for all planned secondary measures are not posted in the secondary results summarized in the record.

The record describes follow-up through Week 24, so it does not establish longer-term outcomes. It also does not report death counts in the safety record. Adverse-event counts are descriptive and cannot alone establish treatment causality or provide a complete comparative safety assessment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Lixisenatide Versus Placebo on Top of Basal Insulin and/or Oral Antidiabetic Treatment in Older Type 2 Diabetic Patients — NCT01798706.
• Registry record last updated 2017-04-18; status last verified 2017-03.
• Results first posted 2016-10-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT01798706 was a randomized, phase 3, double-blind, placebo-controlled, parallel-group, multicenter study of lixisenatide versus placebo in older patients with type 2 diabetes inadequately controlled on their current treatment. The study assessed treatment over 24 weeks, with antidiabetic background therapy.

The primary endpoint was change in HbA1c from baseline to Week 24. The sponsor reported an ANCOVA least-squares mean difference of -0.64, with a 95% confidence interval from -0.81 to -0.464 and p < 0.001. The posted secondary results broadly align with the direction of the primary finding, but multiplicity handling is not reported. Primary missing data were imputed using LOCF.

The registry lists enrollment as 350 and status as completed. The original sample-size justification, full analysis plan, and longer-term results are not reported in the registry record.