A Study to Examine the Effects of Exenatide Once-Weekly Injection on Glucose Control and Safety in Asian Subjects: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Examine the Effects of Exenatide Once-Weekly Injection on Glucose Control and Safety in Asian Subjects (NCT00917267), a randomized phase 3 study. The primary outcome is Change in HbA1c From Baseline to Week 26..

2. Clinical Question

3. Trial Design

The registry identifies this as a Phase 3, randomized, comparator-controlled study with a parallel-group model. It compared exenatide once weekly with exenatide twice daily and used no masking. The registry lists an enrollment of 691. That enrollment figure is not the same as the endpoint-specific analysis counts: the primary results list 307 for exenatide once weekly and 263 for exenatide twice daily. The registry record does not explain the relationship between the overall enrollment and those analysis counts.

The study title and official title describe Asian subjects with type 2 diabetes, with the official title specifying management with oral antidiabetic medications. The brief summary says earlier studies had been conducted in non-Asian populations and that this study was developed to support local regulatory requirements of China, Korea, Japan, India, and Taiwan. This describes the stated context for the study; it does not establish the composition of the enrolled population by country. Country-specific enrollment is not reported in the registry record.

The recorded start was 2009-07, primary completion was 2010-09, and status is completed. The primary endpoint was change in HbA1c from baseline to Week 26. Other listed outcomes cover HbA1c target attainment, fasting serum glucose, body weight, cholesterol measures, triglycerides, and blood pressure. The registry record does not report the randomization procedure, allocation concealment, site details, or the trial’s original sample-size justification. It also does not report the protocol’s planned interim analyses or full statistical analysis plan.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population: Randomized patients received at least one dose of study drug. Only patients with non-missing baseline value and at least one non-missing post-baseline value of the response variable were included in analysis.

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 Change in HbA1c From Baseline to Week 26., measured over Baseline, Week 26.

The primary endpoint is change in HbA1c from baseline to Week 26, measured as a percentage of total hemoglobin. HbA1c is a measure of glycated hemoglobin and is used in clinical research as an indicator of glucose control over time. That general context explains why it can serve as a trial endpoint; it does not add an outcome beyond the registry’s stated measure.

The registry reports the endpoint as a least-squares mean change, with standard error as the measure of dispersion. A change score expresses how the endpoint differs from baseline at the specified follow-up. Negative changes in the posted results indicate decreases from baseline. A least-squares mean is a model-based group estimate; it is not necessarily the same as a simple arithmetic average. The exact model specification and covariates used for the primary endpoint are not reported in the registry record.

The endpoint’s timeframe is baseline to Week 26. This makes the result specific to that assessment point; it does not describe HbA1c changes at later follow-up. The analysis population is described as randomized patients who received at least one dose and had a non-missing baseline result and at least one non-missing post-baseline result for the response variable. The registry record does not report further details about how missing values were handled or how the least-squares means were estimated.

7. Results Posted in the Registry

• Exenatide Twice Daily: mean -1.12 versus -1.43 on control; difference 0.31 (95% CI 0.12 to 0.50), standardized effect d = 0.26; z-test p = 0.002.

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.

Percentage of Patients Achieving HbA1c Targets <=7% at Week 26

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Exenatide Twice Daily: 35.7% (119/333) versus 46.7% (155/332) on control; risk difference -11.0 percentage points (95% CI -18.4 to -3.5), risk ratio 0.77 (0.64–0.92); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Exenatide Twice Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Patients Achieving HbA1c Targets <=6.5% at Week 26

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Exenatide Twice Daily: 15.5% (52/335) versus 26.0% (88/338) on control; risk difference -10.5 percentage points (95% CI -16.6 to -4.4), risk ratio 0.60 (0.44–0.81); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Exenatide Twice Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Fasting Serum Glucose (FSG) From Baseline to Week 26

• 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:
  • Exenatide Twice Daily: mean -23.90 versus -40.57 on control; difference 16.67 (95% CI 10.00 to 23.34), standardized effect d = 0.41; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Exenatide Twice Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span HbA1c target attainment, fasting serum glucose, body weight, cholesterol measures, triglycerides, and blood pressure. The listed targets include HbA1c at or below 7% and at or below 6.5% at Week 26. The posted quantitative results for the two target outcomes and fasting serum glucose are directionally consistent with the primary endpoint comparison: the once-weekly group has higher reported target-attainment percentages and a more negative estimated change in fasting serum glucose. These results provide related measures of glucose control, but they remain distinct endpoints with their own analysis populations and methods.

The registry lists additional secondary outcomes, but results for body weight, cholesterol measures, triglycerides, and blood pressure are not reported in the registry record information available for this analysis. The registry record indicates that nine secondary outcomes were posted, but it does not provide complete result details for every named outcome in the information. Consequently, the overall secondary-outcome pattern cannot be characterized beyond the posted quantitative results.

Secondary analyses generally carry less weight than a prespecified primary analysis when many outcomes are examined, because the chance of at least one apparently notable result can increase across multiple tests. General explanation: multiplicity procedures can address this issue by adjusting inference or by specifying a hierarchy of hypotheses. The registry record does not report whether a multiplicity strategy was used. The secondary results are therefore best read as supporting context, not as independent confirmation that the primary finding applies to every related measure. They also do not establish a broader pattern for outcomes whose numerical results are not reported.

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

• Percentage of Patients Achieving HbA1c Targets <=7% at Week 26
• Percentage of Patients Achieving HbA1c Targets <=6.5% at Week 26
• Change in Fasting Serum Glucose (FSG) From Baseline to Week 26
• Change in Body Weight (BW) From Baseline to Week 26
• Change in Total Cholesterol (TC) From Baseline to Week 26
• Change in High-Density Lipoprotein (HDL) From Baseline to Week 26
• Ratio of Triglycerides (TG) at Week 26 to Baseline
• Change in Blood Pressure From Baseline to Week 26

9. Statistical Interpretation

10. Statistical Methods Explained

General explanation: a randomized parallel-group trial assigns participants to treatment groups and compares outcomes between those groups. Random assignment can support a causal comparison when the design and analysis are appropriate, but it does not remove the need to examine the conduct, missing data, analysis population, and outcome definitions. The registry identifies this study as randomized and parallel-group, but the specific randomization procedure and allocation concealment are not reported in the registry record.

What does a least-squares mean describe?

The primary outcome is reported as a least-squares mean change. In general, a least-squares mean is an estimate from a statistical model rather than necessarily a raw arithmetic mean. Such estimates can account for variables included in the model. The registry record does not identify the covariates or full model specification for the primary endpoint, so the precise adjustments behind the primary group estimates cannot be reconstructed from the posted information. The reported standard error describes uncertainty around each group estimate under the model used; it is not the spread of individual participant outcomes.

How should the between-group estimates be read?

A between-group difference depends on the order of subtraction. The recalculation reports twice daily minus once weekly, yielding 0.31; the sponsor’s analysis reports a negative 0.31 in the reverse direction. These values express the same directional contrast using different orderings, rather than contradictory directions. Because the endpoint is change from baseline, the group estimates are negative, and a positive twice-daily-minus-once-weekly contrast means the twice-daily group’s estimated change is less negative. The sponsor’s estimate is a least-squares mean difference from mixed models analysis. The recalculated estimate is an unadjusted contrast from posted summary statistics and is not the same analysis.

General explanation: a standard error quantifies the estimated uncertainty of a statistic, such as a mean estimate. A confidence interval combines the estimate with uncertainty to give a range of values compatible with the data and the interval procedure. It is not a range containing a known proportion of individual outcomes, and it is not a probability statement about a fixed parameter after the interval has been calculated. The primary group standard errors are reported, while the group-specific confidence limits are not reported in the registry record. The sponsor does report a confidence interval for the between-group estimate.

What do the p-values say?

General explanation: a p-value measures how incompatible the observed data are with a specified null hypothesis under the statistical model and its assumptions. It does not measure the probability that the null hypothesis is true, the size or clinical importance of an effect, or the probability that a result will replicate. The recalculated primary contrast has p = 0.002, while the sponsor reports p < .001. These values come from different analyses, so they should not be treated as interchangeable estimates of one identical procedure. The registry record does not report the full hypothesis-testing plan or a multiplicity adjustment for the trial’s outcomes.

The sponsor labels its analysis non-inferiority or equivalence. General explanation: non-inferiority testing assesses whether a treatment is not worse than a comparator by more than a prespecified margin; equivalence testing asks whether a difference lies within prespecified bounds. These questions require a margin or bounds and a specified testing framework. The margin, the analysis details needed to distinguish the objective, and the protocol’s decision criteria are not reported in the registry record. The label alone is not enough to reconstruct those elements.

What is the role of the recalculation?

The recalculated contrast uses posted summary statistics and is explicitly unadjusted. For the continuous primary endpoint, the calculation uses the reported group estimates and standard errors, with an approximate pooled standard deviation also listed for standardized-effect and planning calculations. Because this is a summary-statistic calculation, it cannot reproduce participant-level modeling, covariate adjustment, or missing-data handling. The primary comparison’s discrepancy flag is false, but the recalculation remains a separate unadjusted analysis and should not replace the sponsor’s reported model-based result.

General explanation: when data are more variable than a simple model allows, standard errors and p-values can be misleading unless the analysis accounts for that extra variability. This is often called over-dispersion, particularly for count or binary data. The primary endpoint is continuous, and the registry record does not report an over-dispersion assessment. This concept should not be taken as a claim that over-dispersion occurred in this trial.

The posted secondary outcomes include both continuous measures and binary target-attainment measures. General explanation: a continuous comparison concerns estimated differences in a measured quantity, while a binary comparison concerns the proportion meeting a defined condition. The posted binary outcomes use HbA1c thresholds at Week 26. Different outcomes may have different analysis populations and sample counts, so each estimate must be read with its own denominator and method. The registry record does not provide the full analysis specifications for every secondary outcome.

11. Confidence Intervals and Precision

The recalculated primary between-group estimate is 0.31, with a 95% confidence interval from 0.116 to 0.504. This interval describes uncertainty around the unadjusted contrast under the recalculation’s assumptions. Its positive direction follows the twice-daily-minus-once-weekly ordering. It is not a prediction interval for individual changes and does not show the range of responses among participants.

The sponsor’s mixed models analysis reports −0.31, with a 95% confidence interval from −0.49 to −0.14. This is the same directional comparison expressed in the reverse order. The sponsor’s interval is on the negative side of zero, while the recalculated interval is on the positive side of zero because of that reversed contrast. The registry record reports p < .001 for the sponsor analysis and p = 0.002 for the unadjusted recalculation; the different analysis methods and reported precision should remain distinct.

General explanation: a confidence interval gives a range of estimates compatible with the data and the procedure used to calculate it. Narrower intervals indicate greater statistical precision for the estimated contrast, while wider intervals indicate more uncertainty. Precision is not the same as clinical importance, absence of bias, or applicability to another population. A confidence interval also does not show the distribution of individual outcomes.

The registry gives standard errors of 0.07 for each primary group estimate but does not report confidence intervals for those individual group estimates. The comparison interval is more directly informative about uncertainty in the difference between groups. Its interpretation still depends on the analysis model and assumptions. The recalculated interval is not a substitute for the sponsor’s mixed-model interval, and neither interval resolves limitations arising from unreported analysis details or missing observations.

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 events. The outcomes represented in these calculations are not time-to-event outcomes. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. These are planning illustrations based on the observed effects, not the trial’s original design assumptions. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design that would have 80% power to detect the specified effect under those planning assumptions. The 90% power column gives the corresponding participants per arm for 90% power. In general, power is the probability of detecting an effect of the specified size if that effect is present, under the assumed model and design. Higher target power generally requires more participants for a given effect and set of assumptions.

Rows that plan for a smaller fraction of the observed effect require more participants per arm than rows using the full observed effect. This follows because smaller effects are harder to distinguish from random variation at a given sample size. The figures are hypothetical design illustrations, not a recommendation for a future study and not a reconstruction of the design used for this trial. They are not observed power. Observed power would not provide a useful substitute for reading the estimated effects and confidence intervals; the planning display instead shows how assumed effect size and target power relate under the stated assumptions.

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 = 0.310; pooled standard deviation σ = 1.185.
2. n = 2 × (1.96 + 0.842)² × 1.185² / 0.310² = 229.5, rounded up to 230 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 <- 0.31                      # observed difference in means
sigma <- 1.18526398081835                     # 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(917267)
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 = 230 (80% power), 308 (90% power)
 75% of observed effect: n per arm = 408 (80% power), 547 (90% power)
 50% of observed effect: n per arm = 918 (80% power), 1,229 (90% power)
power.t.test: 230.4 
Simulated power at n = 230 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 sponsor reports a mixed models analysis for the primary endpoint, with a least-squares mean difference of −0.31, a 95% confidence interval from −0.49 to −0.14, and p < .001. The sponsor’s contrast is expressed as once weekly minus twice daily, so its sign is opposite to the recalculated contrast, which is expressed as twice daily minus once weekly. Read in their respective directions, the estimates describe a consistent ordering of the group changes.

The recalculation is an unadjusted re-analysis of posted summary statistics. It gives a difference of 0.31, a 95% confidence interval from 0.116 to 0.504, and p = 0.002. It does not reproduce the sponsor’s mixed models analysis, whose model specification and covariates are not reported in the registry record. The comparison of the estimates should therefore focus on their direction after accounting for group order, and on the fact that the methods differ, rather than treating the p-values or intervals as identical outputs.

The registry labels the sponsor’s analysis as non-inferiority or equivalence. The margin and details needed to interpret that objective are not reported in the registry record. The discrepancy flag is false, but the recalculation remains a separate unadjusted analysis; it should not be presented as replacing the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry describes the primary analysis population as randomized patients who received at least one dose of study drug and had a non-missing baseline value and at least one non-missing post-baseline value for the response variable. This is the stated population definition for the primary endpoint. The registry record does not report additional details on imputation, sensitivity analyses, or how missing outcome values were handled. It also does not report the number or reasons for missing observations by group.

The endpoint-specific analysis counts differ across the primary and secondary outcomes. This can occur when outcomes have different availability or analysis populations, but the registry record does not give enough detail to identify the reasons for the particular counts. The overall enrollment figure should not be treated as the denominator for every endpoint; each analysis has its own reported counts.

The registry lists several secondary outcomes and multiple analyses. The statistical plan for controlling multiplicity, including any adjustment to significance thresholds or ordering of hypotheses, is not reported in the registry record. As a result, the posted p-values for secondary outcomes should not automatically be interpreted as if they were adjusted for the full family of comparisons. The protocol’s interim-analysis plan is also not reported in the registry record.

The randomization method, allocation concealment, covariates for the primary model, and detailed model specifications are not reported in the registry record. The trial is described as unmasked, so masking cannot be assumed to have reduced the potential for performance or assessment influences. These missing design and analysis details limit independent reconstruction of the sponsor’s analysis. The registry record does identify the primary outcome, timeframe, reported group estimates, and sponsor comparison, but it does not give a complete statistical analysis plan.

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: cerebral infarction (0.6%), acute myocardial infarction (0.3%), ankle fracture (0.3%), aortic aneurysm (0.3%), ileus (0.3%).

The registry reports serious adverse events for 13 of 340 participants at risk in the exenatide once-weekly group and 8 of 338 participants at risk in the exenatide twice-daily group. Other adverse events are reported for 131 of 340 and 150 of 338 participants at risk, respectively. These are descriptive counts and denominators from the registry; they are not a complete comparative safety analysis. No rates or between-group safety contrasts are calculated.

The most frequently listed serious-event terms include cerebral infarction at 0.6%, and acute myocardial infarction, ankle fracture, aortic aneurysm, ileus, and pneumonia at 0.3% each. These percentages are reproduced as recorded. The registry does not provide event timing, severity grading beyond the serious-event classification, exposure-adjusted rates, or detailed causal assessments in the information available for this analysis.

Deaths are not reported in the registry record. The serious and other adverse-event counts should be interpreted within the reported at-risk groups and alongside the limits of the available safety detail. They do not, on their own, establish that either treatment is safer or less safe.

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

The primary results show decreases in HbA1c from baseline to Week 26 in both treatment groups, with a difference between the group estimates. The sponsor’s mixed-model estimate and the unadjusted recalculation express the comparison in opposite directions and use different methods. Together, they describe the posted statistical comparison, not a complete account of every participant’s outcome or a guarantee of what would be observed in another setting.

The results apply to the study population and timeframe described in the registry: Asian subjects with type 2 diabetes, with the official title specifying management with oral antidiabetic medications, and a primary assessment at Week 26. They do not establish that the same estimates apply to people outside that population, to other treatment schedules, or to later follow-up. Country-specific composition and later endpoint results are not reported in the registry record.

A statistically detectable difference is not by itself a judgment about clinical importance. The registry does not provide a threshold for a clinically meaningful HbA1c difference, and none should be inferred from the p-value alone. The sponsor’s non-inferiority or equivalence label also cannot be fully evaluated without the margin and analysis criteria, which are not reported in the registry record.

The endpoint results do not replace a full evaluation of safety, the secondary outcomes, or study limitations. Some secondary results are available and align directionally with the primary comparison, while results for other named measures are not reported in the registry record. Safety counts are descriptive and deaths are not reported in the registry record. The findings should therefore be understood as evidence about the specified endpoint and comparison, with uncertainty and reporting limitations, rather than a general treatment recommendation.

18. Why This Trial Matters Statistically

This trial is statistically informative because it reports both group-level changes in HbA1c and a sponsor-estimated between-group contrast, with an interval and p-value for the primary comparison. Reporting the group estimates alongside the contrast helps distinguish change within each group from the difference between groups. The sign of a contrast depends on group order, an important detail when comparing the sponsor analysis with the unadjusted recalculation.

The trial also illustrates why method matters. The sponsor used mixed models analysis and reported least-squares mean difference, while the recalculation is unadjusted and based on posted summary statistics. These estimates should not be mistaken for outputs from the same model. The endpoint-specific analysis counts also show why enrollment and analyzed populations are not interchangeable, and why outcome denominators should be read with each result.

The study’s stated context is evaluation in Asian subjects after earlier once-weekly exenatide studies had been conducted in non-Asian populations. This gives the population focus statistical relevance, while the absence of country-specific enrollment details limits assessment of how broadly the enrolled sample represents the named settings. Its unmasked design, the lack of a reported multiplicity plan, and missing details about the analysis model also matter when interpreting precision and generalizability.

Finally, the registry’s planning illustrations demonstrate how assumed effect size and desired power relate to participants per arm. They are not evidence about the trial’s original design or its observed power. Taken together, the record supports careful reading of the estimate, its uncertainty, the analysis population, and what the registry does not report.

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 identifies the study as unmasked. The information available does not describe steps used to reduce potential bias in outcome assessment or treatment management. The randomization procedure and allocation concealment are not reported in the registry record, limiting assessment of how assignment was implemented.

The primary endpoint is reported at Week 26, and later HbA1c follow-up is not reported in the registry record. The study’s brief summary gives a regional regulatory context, but country-specific enrollment and the characteristics of participants by country are not reported. This restricts assessment of how representative the enrolled group was across the named settings.

The primary analysis population requires a non-missing baseline value and at least one non-missing post-baseline value for the outcome. Further missing-data methods, reasons for missingness, and sensitivity analyses are not reported in the registry record. The model specification, covariates, and randomization details are also absent, so the sponsor’s primary analysis cannot be independently reconstructed from the registry information available.

Several secondary outcomes are named, but detailed numerical results are not reported for all of them in the available record. The multiplicity strategy is not reported, and the sponsor’s non-inferiority or equivalence label is not accompanied by a reported margin or decision criteria. Safety information is descriptive, and deaths are not reported in the registry record. These limitations constrain conclusions about the full outcome profile; they do not negate the reported primary estimates, but they narrow what can be inferred from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Examine the Effects of Exenatide Once-Weekly Injection on Glucose Control and Safety in Asian Subjects — NCT00917267.
• Registry record last updated 2015-04-09; status last verified 2015-03.
• Results first posted 2012-12-31.
• 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 registry describes a completed Phase 3 randomized, open-label, parallel-group study comparing exenatide once weekly with exenatide twice daily in Asian subjects with type 2 diabetes. The primary endpoint was change in HbA1c from baseline to Week 26. The posted least-squares mean changes were −1.43 and −1.12, respectively, with standard errors of 0.07. The sponsor reported a mixed-model difference of −0.31 with a 95% confidence interval from −0.49 to −0.14 and p < .001.

The unadjusted recalculation expresses the contrast in the reverse direction and reports 0.31, a 95% confidence interval from 0.116 to 0.504, and p = 0.002. The registry also lists secondary glucose, metabolic, and safety outcomes, though results are not reported for every named outcome in the available record. The registry record does not report the full analysis plan, multiplicity approach, or several details needed to reconstruct the sponsor’s methods.