Safety and Efficacy Study of Exenatide Once Weekly in Adolescents With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of Exenatide Once Weekly in Adolescents With Type 2 Diabetes (NCT01554618), a randomized phase 3 study. The primary outcome is Change From Baseline in Glycosylated Hemoglobin A1c (HbA1c) to Week 24 (Controlled Assessment Period).

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group, multicenter study sponsored by AstraZeneca. The registry describes quadruple masking. The intervention arms were exenatide once weekly and placebo once weekly. The registered enrollment was 84, while the primary efficacy results list 58 patients in the exenatide group and 24 in the placebo group. Those endpoint analysis counts should not be treated as a complete account of enrollment or of why participants may not have contributed to the endpoint analysis.

The primary outcome was change from baseline in HbA1c to Week 24 in the controlled assessment period. Baseline was defined as the last non-missing assessment, scheduled or unscheduled, on or before the first dose of randomized study medication. The reported mixed model with repeated measures excluded data collected after rescue medication began or study medication was prematurely discontinued. The registry identifies an Evaluable Analysis Set for this endpoint, based on randomization, receipt of at least 1 dose, and baseline and post-baseline HbA1c assessments.

The record lists secondary outcomes covering fasting plasma glucose, body weight, fasting insulin, HbA1c goal attainment, lipid profiles, systolic and diastolic blood pressure, rescue medication, and measures of beta-cell function and insulin sensitivity. It records 23 outcome measures, 11 analyses, and 20 posted secondary outcomes. The trial is marked completed. The record does not report the original sample-size justification, planned allocation ratio, detailed visit schedule beyond the endpoint timeframe, or the trial’s full statistical analysis plan. These omissions limit how much can be inferred about the design choices before results were known.

4. Participant Flow and Accounting

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

Before assignment: Study had a screening period (5 weeks), controlled assessment period (24 weeks; patients randomized 5:2 to exenatide or placebo), open-label extension period (28 weeks) and post-treatment follow-up period (10 weeks). 84 patients were randomized but 1 due to clinical error and immediately discontinued, thus, 83 patients were included in the study.

Randomized Through Start of Treatment

Reasons for not completing this period:

Controlled Assessment Period

Reasons for not completing this period:

Open-Label Extension Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Evaluable Analysis Set consisted of all randomized patients who received at least 1 dose of randomized study medication and had at least 1 baseline and post-baseline HbA1c assessment.

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: Baseline analysis performed on Intent-to-Treat (ITT) Analysis Set which consisted of all randomized patients who received at least 1 dose of randomized study medication.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Glycosylated Hemoglobin A1c (HbA1c) to Week 24 (Controlled Assessment Period), measured over Baseline (Week 0) and Week 24.

The primary endpoint is the change from baseline in glycosylated hemoglobin A1c (HbA1c) to Week 24 during the controlled assessment period, expressed in percentage (% HbA1c). It is a continuous outcome: each participant’s follow-up value is considered relative to their baseline value, and the reported group summaries are adjusted least-squares means. The endpoint description defines baseline as the last non-missing assessment on or before the first dose of randomized study medication.

HbA1c is used in diabetes trials because it captures glycemic exposure over time rather than a single glucose measurement. As a general statistical point, a continuous outcome can retain information about the range of observed changes; it does not reduce all results to whether a participant crossed a chosen threshold. The registry separately lists secondary outcomes involving whether HbA1c goals were achieved, but those are different questions from the primary mean-change comparison.

The endpoint analysis used a mixed model with repeated measures and excluded observations after initiation of rescue medication or premature discontinuation of study medication. Those choices define what the reported estimate represents: a model-based comparison using the specified assessment data and analysis population, not a summary of every measurement regardless of what happened after randomization.

7. Results Posted in the Registry

• Controlled Assessment Period - Placebo: mean 0.49 versus -0.36 on control; difference 0.85 (95% CI 0.20 to 1.50), standardized effect d = 0.61; z-test p = 0.010.

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 From Baseline in Fasting Plasma Glucose (FPG) Concentration to Week 24 (Controlled Assessment Period)

• 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:
  • Controlled Assessment Period - Placebo: mean 16.50 versus -5.20 on control; difference 21.70 (95% CI -5.08 to 48.48), standardized effect d = 0.38; z-test p = 0.112.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Controlled Assessment Period - Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Body Weight to Week 24 (Controlled Assessment Period)

• 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:
  • Controlled Assessment Period - Placebo: mean 0.63 versus -0.59 on control; difference 1.22 (95% CI -1.10 to 3.54), standardized effect d = 0.24; z-test p = 0.304.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Controlled Assessment Period - Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Fasting Insulin to Week 24 (Controlled Assessment Period)

• 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:
  • Controlled Assessment Period - Placebo: mean -15.30 versus 79.60 on control; difference -94.90 (95% CI -279.74 to 89.94), standardized effect d = -0.24; z-test p = 0.314.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Controlled Assessment Period - Placebo and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes across glycemic measures, body weight, insulin, HbA1c goal attainment, lipids, blood pressure, rescue medication, and measures of beta-cell function and insulin sensitivity. The posted continuous secondary comparisons cover fasting plasma glucose, body weight, and fasting insulin. Their estimated directions are not uniform, and the reported confidence intervals include zero. Overall, the secondary results are less conclusive than the primary HbA1c result and do not form a uniformly precise pattern.

These outcomes provide additional context about other measures considered during the controlled assessment period, but they are not substitutes for the primary endpoint. The primary analysis was defined as change in HbA1c, whereas each secondary outcome addresses a distinct measure or event. The registry record does not report results for every listed secondary outcome in the details available for interpretation, and a listed outcome should not be assumed to have a particular result unless that result is posted.

Unadjusted secondary results carry less inferential weight when multiple outcomes are examined. As a general statistical issue, testing many outcomes increases the opportunity to observe a nominally notable result by chance. A prespecified testing hierarchy or a multiplicity adjustment can help control that risk; such a strategy is not reported in the registry record. Therefore, secondary results are best treated as supporting or hypothesis-generating evidence rather than as independent confirmation of the primary finding.

The secondary estimates also have their own uncertainty and analysis details. Their group sizes are not identical to the primary outcome’s broader trial enrollment, and the listed endpoint analysis counts should be read for each outcome rather than assumed to apply to all measures. A consistent overall interpretation requires attention to outcome definitions, available observations, and the possibility that different measures capture different aspects of glycemic and metabolic status.

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

• Change From Baseline in Fasting Plasma Glucose (FPG) Concentration to Week 24 (Controlled Assessment Period)
• Change From Baseline in Body Weight to Week 24 (Controlled Assessment Period)
• Change From Baseline in Fasting Insulin to Week 24 (Controlled Assessment Period)
• Percentage of Patients Achieving HbA1c Goals of < 6.5%, ≤ 6.5%, and < 7.0% at Week 24 (Controlled Assessment Period)
• Change From Baseline in Lipid Profiles to Week 24 (Controlled Assessment Period)
• Change From Baseline in Systolic Blood Pressure (SBP) and Diastolic Blood Pressure (DBP) to Week 24 (Controlled Assessment Period)
• Number of Patients Needing Rescue Medication Due to Failure to Maintain Glycemic Control up to Week 24 (Controlled Assessment Period)
• Change From Baseline in Homeostasis Model Assessments - Beta-Cell Function (HOMA-B) and Insulin Sensitivity (HOMA-S) to Week 24 (Controlled Assessment Period)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is reported as an adjusted least-squares mean contrast from a mixed model with repeated measures (MMRM). A repeated-measures model handles outcome observations taken at multiple time points by modeling their relationship within a participant, rather than treating every measurement as unrelated. As a general statistical explanation, this can use longitudinal information while accounting for correlation among repeated measurements. The registry record does not report the model’s full specification, including its covariance structure, fixed effects, or any covariates beyond what is stated in the endpoint description.

What does an adjusted least-squares mean represent?

A least-squares mean is a model-based estimate of a group mean, adjusted according to the model’s terms. It is not necessarily identical to a raw arithmetic mean. The registry reports adjusted least-squares mean changes of -0.36 for exenatide and 0.49 for placebo. The corresponding sponsor-reported LS mean difference is -0.85. The direction depends on which group is subtracted from which; the sponsor’s negative value expresses the contrast in its stated orientation, while a placebo-minus-exenatide contrast has the opposite sign.

Adjustment can improve comparability when a model accounts for relevant features of the design or repeated measurements. It also makes interpretation dependent on the model specification. The registry provides the MMRM label and the endpoint’s assessment rules, but not enough detail to reconstruct every modeling choice. Therefore, the sponsor estimate should be interpreted as the reported model-based estimate, rather than as a fully independently reproducible analysis.

Why might the recalculation differ from the reported model?

The recalculated comparisons use posted arm-level estimates and standard errors to produce a simple, unadjusted comparison. For these calculations, the posted standard errors are used to approximate variability; the reported re-calculation notes that the pooled standard deviation is approximate. This is a different procedure from fitting the sponsor’s MMRM to participant-level repeated observations. A summary-statistic calculation cannot reproduce the longitudinal model’s handling of time, within-participant correlation, covariate adjustment, or analysis-specific observations.

For the primary endpoint, the recalculated contrast and sponsor-reported contrast have matching direction after accounting for the subtraction order, and their magnitudes are close. Their confidence intervals and p-values are also close but not identical. The recalculation is useful as a transparent check on the posted summaries, but it does not have the same analytic status as the sponsor’s model. The record does not mark a discrepancy between the calculations.

What does a confidence interval add?

A confidence interval conveys uncertainty around an estimate. In general, a 95% confidence procedure is designed so that, over repeated applications under its assumptions, intervals would cover the target parameter at the stated rate. For a particular trial, the interval is not a probability statement that the true value lies in a specific range. It provides a range of values compatible with the data and method, and its width indicates how precisely the effect is estimated.

For a difference in means, zero represents no difference on the scale of the contrast. An interval that includes zero does not provide clear evidence of a difference at the conventional two-sided 0.05 threshold; an interval that excludes zero is consistent with a nonzero contrast under the analysis. This convention does not measure clinical importance. A narrow interval can still include values whose practical importance is uncertain, and a statistical result does not resolve the relevance of the endpoint to patients.

How should p-values be understood?

A p-value describes how unusual data at least as incompatible with a specified null model would be, if that model and the analysis assumptions held. It is not the chance that the result occurred by random error alone, and it is not an effect-size measure. The sponsor-reported primary p-value is 0.012. The unadjusted p-value attached to the simple summary-statistic re-calculation is 0.01. The slight difference is unsurprising because the procedures are not identical; the model-based analysis remains the sponsor’s reported analysis.

For secondary comparisons, the posted re-calculated p-values are unadjusted and arise from separate comparisons. When many outcomes are examined, the chance of at least one apparently notable result can rise. A multiplicity adjustment or a prespecified hierarchy can address that issue, but the registry record does not report such a strategy for these results. General statistical caution therefore applies: secondary p-values should not be interpreted as if each were the sole planned test.

What do the analysis population and exclusions mean?

The primary endpoint population consists of randomized patients who received at least 1 dose and had baseline and post-baseline HbA1c assessments. The model excluded data collected after rescue medication began or study medication was prematurely discontinued. This is a defined analysis, rather than an all-randomized analysis that necessarily incorporates every post-randomization observation. Rescue medication and discontinuation can be associated with outcome trajectories, so the handling of these events matters to interpretation.

MMRM methods commonly rely on assumptions about the pattern of missing observations and the model used for observed measurements. That is a general property of longitudinal modeling, not a claim about the specific missing-data mechanism in this trial. The registry record does not report the amount or pattern of missing endpoint data, sensitivity analyses, or a detailed imputation strategy. The reported estimate should consequently be interpreted within the stated population and data exclusions, without assuming unreported procedures.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is an LS mean difference of -0.85, with a 95% confidence interval from -1.51 to -0.19. The interval does not include zero, so it supports a nonzero contrast under the reported model and its assumptions. Its endpoints also show that the estimated effect is uncertain: values across the interval remain compatible with the data at the stated confidence level. The interval does not indicate which values would be clinically important; the registry record does not give a clinical-importance threshold.

The simple unadjusted re-calculation gives a placebo-minus-exenatide difference of 0.85 and a 95% interval from 0.205 to 1.495. Its orientation is opposite to the sponsor’s reported contrast, and it uses approximate variability derived from posted summaries. The two results are close in magnitude after aligning direction, but they are not the same analysis. For inference about the trial, the sponsor’s MMRM result is the central reported estimate.

For the posted secondary continuous comparisons, the reported 95% confidence intervals span zero. In general, this means that the data are compatible with no difference as well as with differences in either direction within the interval. Broad intervals indicate limited precision, while even narrower intervals do not by themselves establish clinical relevance. The secondary results should be read as uncertain estimates, not as proof of no effect or proof of a meaningful effect.

Precision is influenced by the amount and variability of observed data and by the analysis method. The registry record reports endpoint group counts and standard errors, but does not report all details needed to separate the contribution of each source of uncertainty. Confidence intervals are therefore more informative than a binary reading of statistical significance, while remaining conditional on the model and the analysis population.

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 illustrations give participants per arm for these continuous-outcome comparisons; they are not totals across arms and are not total event counts. The registry record’s stated 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 original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% probability of detecting the specified effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target probability of detection under the same planning framework. These are prospective planning quantities, not descriptions of how likely the completed trial was to find a result after its data had been observed. This is not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm than rows planning for the full observed effect. That is a general feature of power calculations: smaller differences are harder to distinguish from sampling variation, so larger samples are generally needed. The figures are illustrations based on an effect estimated from this trial, not evidence that a future trial will observe that effect or reproduce the same uncertainty.

The calculations also assume equal allocation even though the posted endpoint analysis group counts differ. The illustrations should therefore be treated as a standardized planning comparison rather than as a reconstruction of the trial’s actual design. They do not account for any unreported design features, missing data, multiplicity strategy, or other adjustments. Their usefulness is to show how the required per-arm sample size changes when the target effect or desired power changes, not to establish a definitive sample size for a future study.

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 = 0.850; pooled standard deviation σ = 1.383.
2. n = 2 × (1.96 + 0.842)² × 1.383² / 0.850² = 41.6, rounded up to 42 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 <- 0.85                      # observed difference in means
sigma <- 1.3832386995743                     # 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(1554618)
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 = 42 (80% power), 56 (90% power)
 75% of observed effect: n per arm = 74 (80% power), 99 (90% power)
 50% of observed effect: n per arm = 167 (80% power), 223 (90% power)
power.t.test: 42.6 
Simulated power at n = 42 per arm: 0.797 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analysis uses a mixed model with repeated measures and reports an LS mean difference of -0.85, a 95% confidence interval from -1.51 to -0.19, and p = 0.012. This is the study’s stated model-based result for the primary endpoint. The calculation based on posted arm summaries reports the contrast in the reverse direction as placebo minus exenatide: 0.85, with a 95% interval from 0.205 to 1.495 and an unadjusted p-value of 0.01.

The sign difference is a matter of contrast orientation, not contradictory direction: reversing the order of subtraction reverses the sign. The two methods also use different information and assumptions. The recalculation uses arm-level summaries and approximate variability; it does not refit the sponsor’s repeated-measures model. Small differences in interval limits and p-values therefore do not establish an inconsistency.

The registry record does not flag a discrepancy. The sponsor’s reported result should be used when describing the trial’s own analysis, while the recalculation can serve as a secondary check on the posted summaries. Neither should be interpreted without the endpoint definition, evaluable population, post-rescue and discontinuation exclusions, and uncertainty shown by the confidence interval.

15. Multiplicity, Missing Data and Analysis Populations

The record includes a primary HbA1c outcome and a broad set of secondary outcomes. It reports 23 outcome measures, 11 analyses, and 20 posted secondary outcomes. Considering several outcomes creates a multiplicity issue: even when each test uses a conventional threshold, the chance of at least one apparently positive result can rise as the number of tests increases. This is a general statistical concern, not a claim that any specific result is false.

The registry record does not report whether secondary outcomes were controlled using a family-wise error procedure, a false-discovery approach, a hierarchical testing sequence, or another multiplicity plan. It also does not report a prespecified ordering of secondary hypotheses. Accordingly, the secondary p-values should not be treated as if each were a stand-alone confirmatory test. The primary endpoint retains a clearer inferential role because it is identified as primary, but the record does not provide a full statistical analysis plan to establish every prespecification detail.

Missing-data interpretation is also limited. The primary endpoint uses an Evaluable Analysis Set that requires randomization, at least 1 dose, and baseline and post-baseline HbA1c assessments. Its MMRM excludes data after initiation of rescue medication or premature discontinuation of study medication. Those rules are reported, but the record does not report how much data was missing, why measurements were unavailable, the specific assumptions about missingness, or sensitivity analyses that test alternative assumptions.

As a general point, a repeated-measures model can use observed longitudinal data, but the validity of its estimate depends in part on the model specification and assumptions about missing observations. Excluding post-rescue or post-discontinuation data also defines the estimand differently from an analysis that incorporates those outcomes. Without further details, the extent to which these choices affect the estimate cannot be determined from the registry record. These limitations call for cautious interpretation rather than an assumption that missingness or multiplicity had no effect.

16. Safety Results

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

Deaths

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: suicidal ideation (4.5%), irritable bowel syndrome (4.3%), gastritis (2.0%), cellulitis (2.0%), pneumonia (2.0%).

During the controlled assessment period, the registry reports serious adverse events affecting 2 patients at risk in the exenatide group and 1 patient at risk in the placebo group. The corresponding groups at risk were 59 and 23. No deaths were reported in either group during this period. The other-adverse-event counts were 25 and 10, respectively, among those same reported groups at risk.

For the extension period, the exenatide group had 3 serious adverse events among 50 at risk, while the placebo-to-exenatide group had 1 among 22 at risk. No deaths were reported in either extension group. Other adverse events affected 10 and 4, respectively. The extension groups represent a different period and treatment description from the controlled comparison, so they should not be combined with or read as a randomized placebo comparison.

The registry also lists serious adverse event terms and percentages, including suicidal ideation at 4.5% and irritable bowel syndrome at 4.3%. These listings do not by themselves establish causation or comparative risk. Counts are descriptive, and group sizes and follow-up contexts differ across periods. The registry record does not provide enough context to determine relatedness, timing, severity beyond the serious-event classification, or a causal attribution to treatment.

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

The primary result is an estimate of the difference in mean HbA1c change between randomized groups during the controlled assessment period, under the reported analysis. The sponsor’s MMRM estimate has a 95% confidence interval that excludes zero. This supports a statistical difference under that model, but statistical evidence is not the same as proof of clinical importance, durability, or benefit for every participant.

The trial’s result is specific to the population and endpoint analysis described in the registry. The Evaluable Analysis Set required a baseline and post-baseline HbA1c assessment and excluded measurements after rescue medication began or study medication was prematurely discontinued. The registered endpoint was assessed through Week 24; the result does not establish what would happen over a longer period. The registry record does not report a clinically important difference threshold or detailed subgroup results that would support broader claims about who might experience a particular outcome.

A confidence interval communicates uncertainty around the estimated contrast, while a p-value addresses compatibility with a null model under the analysis assumptions. Neither tells a reader whether a particular treatment choice is right for an individual. The interpretation of clinical outcomes also requires consideration of other measures, harms, preferences, and evidence beyond a single endpoint. The posted adverse-event counts are descriptive and do not establish treatment causation.

Thus, the result should be described as a model-based trial finding, not as a universal prediction. It does not prove that the same estimate applies to all adolescents with type 2 diabetes, that differences in secondary measures are established, or that the observed estimate will be reproduced in another study. The result also cannot, on its own, resolve questions about missing data, multiplicity, or unreported aspects of the analysis plan.

18. Why This Trial Matters Statistically

This trial illustrates how an endpoint estimate depends on more than the difference between two group summaries. The primary result is reported as an adjusted least-squares mean contrast from a repeated-measures model, with a defined analysis population and explicit exclusions for observations after rescue medication or premature discontinuation. Understanding those details is essential for knowing what population and data the estimate represents.

It also demonstrates why confidence intervals matter alongside p-values. The reported interval indicates a nonzero contrast under the model while showing a range of uncertainty around the estimate. Secondary comparisons are less precise and do not provide a uniformly clear pattern. Looking across endpoints without considering multiplicity could give undue weight to isolated findings, particularly when the registry does not report a multiplicity strategy.

The trial’s posted arm summaries also allow a simple recalculation that can be compared with the sponsor’s analysis. That comparison is informative only when the difference in methods and sign convention is understood: an arm-level approximation is not equivalent to refitting the sponsor’s MMRM. In this case, the results are close after aligning contrast direction, while the sponsor’s analysis remains the trial’s reported inferential result.

Finally, the planning illustrations show the relationship between target effect size and required sample size under stated assumptions, without establishing the original design rationale or the future performance of a study. Together, these features make the trial useful for learning how design, analysis population, uncertainty, multiplicity, and interpretation interact in clinical biostatistics.

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 primary efficacy analysis is based on an Evaluable Analysis Set rather than a population defined only by randomization. It required receipt of at least 1 dose and baseline and post-baseline HbA1c assessments. The MMRM excluded measurements after rescue medication began or study medication was prematurely discontinued. These features are part of the stated analysis, but the registry record does not report the number or pattern of missing assessments, reasons for missingness, or sensitivity analyses. The robustness of the estimate to alternative missing-data assumptions therefore cannot be assessed from this record.

The endpoint analysis counts differ between the exenatide and placebo groups, and the reported standard errors reflect uncertainty in those estimates. Unequal analyzed group sizes can contribute to unequal precision. The registry record does not explain the reasons for the endpoint counts or provide enough participant-level information to assess whether exclusions affected the groups differently.

The outcome is limited to change in HbA1c through Week 24 for the controlled assessment period. The record does not provide a clinical-importance threshold, detailed participant characteristics, subgroup analyses, or enough information to judge how well the results generalize beyond the studied population. It also does not report the original sample-size justification or complete statistical analysis plan.

Multiplicity is another limitation: several secondary outcomes are listed, but the record does not report an adjustment strategy or testing hierarchy. Secondary results should therefore be interpreted cautiously. Finally, adverse-event counts are descriptive, and the information reported does not establish causality or provide a complete assessment of comparative safety. These trial-specific limitations leave important questions that cannot be resolved from the registry results alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of Exenatide Once Weekly in Adolescents With Type 2 Diabetes — NCT01554618.
• Registry record last updated 2021-11-30; status last verified 2021-10.
• Results first posted 2020-12-03.
• 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

The completed Phase 3 study was randomized, double-blind, placebo-controlled, parallel-group, multicenter, and quadruple-masked. It compared exenatide once weekly with placebo once weekly in adolescents with type 2 diabetes.

The primary outcome was change in HbA1c from baseline to Week 24 during the controlled assessment period. The sponsor-reported MMRM analysis gave an LS mean difference of -0.85, with a 95% confidence interval from -1.51 to -0.19 and p = 0.012. The analysis used an Evaluable Analysis Set and excluded observations after rescue medication or premature discontinuation.

Secondary outcomes covered several glycemic and metabolic measures; their posted continuous comparisons are less conclusive. Serious adverse event counts are reported for controlled and extension periods, with no deaths listed in any group. The registry record does not report the original sample-size justification, full statistical analysis plan, multiplicity strategy, or detailed missing-data sensitivity analyses.