Effect of Chronic Exenatide Therapy on Beta Cell Function and Insulin Sensitivity in T2DM: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Chronic Exenatide Therapy on Beta Cell Function and Insulin Sensitivity in T2DM (NCT02981069), a randomized phase 4 study. The primary outcome is Change in Endogenous Glucose Production (EGP) After Acute Exposure to a Single Dose and Again After 16 Weeks of Treatment.

2. Clinical Question

3. Trial Design

This is a randomized, parallel-group, phase 4 study of treatments in type 2 diabetes. Masking is listed as none, so the registry describes the trial as unmasked. The record lists an enrollment of 90 and a completed study. The recorded study start is 2017-12-15, and the primary completion date is 2022-07-14.

Four groups appear in the posted primary outcome results: exenatide, dapagliflozin, exenatide plus dapagliflozin, and placebo. The reported group sizes for that outcome are 25, 25, 25, and 15, respectively. These are the outcome-specific counts posted in the registry, not a description of how many participants were randomized or retained at every study stage. A participant flow account is not reported in the registry record.

The regimen descriptions identify Byetta and Bydureon for exenatide and Farxiga for dapagliflozin. They describe a 4-week phase followed by a 12-week phase for the active regimens, and a placebo group described across 4 weeks and 12 weeks. The posted primary timeframe, however, is acute exposure after one dose. The outcome title mentions both acute exposure and assessment after 16 weeks; the record does not post a distinct 16-week primary result alongside the acute summaries.

The primary outcome description details a fasting measurement using a prime-continuous infusion of 3-3H-glucose, followed by a tracer equilibration period and administration of a study drug or placebo. The record states that the acute study description anticipated 20 subjects per group, while the posted primary outcome group counts differ. The reason for this difference is not reported in the registry record. Details of random sequence generation, allocation concealment, and adherence are not reported in the registry record.

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: Type 2 diabetes with significant clinical complications were excluded

Acute Portion of Study

16 Week Drug Administration Period

Analysis population for the primary outcome, as defined in the registry: Type 2 diabetes

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 Endogenous Glucose Production (EGP) After Acute Exposure to a Single Dose and Again After 16 Weeks of Treatment, measured over ACUTE [after a single dose of each study drug or placebo].

The primary endpoint is change in endogenous glucose production (EGP), measured in mg/kg.min. EGP refers to glucose entering the circulation from endogenous sources. The study used a tracer method: after an overnight fast, eligible participants received a prime-continuous infusion of 3-3H-glucose, and measurements were collected during a morning procedure. The description specifies an 8.5-hour measurement period and a 3.5-hour tracer equilibration period before study medication or placebo was administered.

EGP is used in this study as a physiological measure related to glucose regulation. Measuring it around acute exposure allows the posted primary comparisons to describe the change recorded after a single dose of each drug or placebo. The reported arm values are means, and the accompanying spread is identified as the standard error. A standard error describes uncertainty in an estimated mean; it is not the range of individual participant values.

The endpoint title refers to measurement after acute exposure and again after 16 weeks of treatment, but the posted primary timeframe is explicitly acute, after a single dose. Therefore, the registry results discussed for the primary outcome concern the acute comparison. A separate estimate for the EGP change after 16 weeks is not reported in the registry record. The record also does not report a detailed primary-endpoint analysis plan or explain how multiple EGP measurements, if any, were combined into the posted change measure.

7. Results Posted in the Registry

• EXENATIDE: mean -0.18 versus -0.03 on control; difference -0.15 (95% CI -0.21 to -0.09), standardized effect d = -1.62; z-test p = <0.001.
• Dapagliflozin: mean 0.14 versus -0.03 on control; difference 0.17 (95% CI 0.10 to 0.24), standardized effect d = 1.33; z-test p = <0.001.
• Exenatide Plus Dapagliflozin: mean -0.08 versus -0.03 on control; difference -0.05 (95% CI -0.12 to 0.02), standardized effect d = -0.39; z-test p = 0.166.

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 Fasting Plasma Glucose (FPG) Concentration

• 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:
  • Dapagliflozin: mean 72.00 versus 42.00 on control; difference 30.00 (95% CI 23.80 to 36.20), standardized effect d = 2.68; z-test p = <0.001.
  • Byetta/Bydureon Plus Dapagliflozin: mean 11.00 versus 42.00 on control; difference -31.00 (95% CI -37.20 to -24.80), standardized effect d = -2.77; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dapagliflozin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Byetta/Bydureon Plus Dapagliflozin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Plasma Glucagon Concentration

• 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:
  • Dapa: mean 5.00 versus 4.00 on control; difference 1.00 (95% CI -4.54 to 6.54), standardized effect d = 0.10; z-test p = 0.724.
  • Exenatide: mean -6.00 versus 4.00 on control; difference -10.00 (95% CI -15.54 to -4.46), standardized effect d = -1.00; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dapa and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Exenatide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Plasma Insulin Concentration

• 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:
  • Dapa: mean -2.00 versus -2.00 on control; difference 0.00 (95% CI -4.38 to 4.38), standardized effect d = 0.00; z-test p = 1.000.
  • Exenatide: mean 3.00 versus -2.00 on control; difference 5.00 (95% CI 0.62 to 9.38), standardized effect d = 0.63; z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dapa and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Exenatide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover fasting plasma glucose, plasma glucagon, and plasma insulin. Together they broaden the physiological picture beyond the acute EGP endpoint, with measurements described at 16 weeks or from baseline to 16 weeks. The overall pattern is not uniform across measures: the posted summaries show contrasts across treatment groups for some outcomes, while other comparisons are less distinct. These results concern different biological measures and timeframes, so they should not be treated as interchangeable evidence about the primary EGP question.

The secondary findings can help readers see whether related measures moved in a pattern that merits further study. They do not resolve the gap between the acute primary result and the 16-week EGP assessment mentioned in the primary endpoint title, because a separate later EGP result is not reported in the registry record. Nor can the secondary means establish a mechanism linking treatment to EGP. The registry summaries do not include participant-level correlations or a reported model connecting these outcomes.

All secondary comparisons are unadjusted recalculations, and the record lists no reported analyses. Multiple outcomes and treatment contrasts create multiple opportunities for nominally unusual results. Without a reported multiplicity strategy, p-values should be viewed as descriptive evidence for each comparison rather than as a family-wise confirmatory conclusion. Their interpretation is further limited by the absence of a reported analysis plan, analysis populations, missing-data handling, or covariate adjustment. The secondary results therefore provide context, but they carry less inferential weight than a prespecified, reported analysis designed around a clearly stated primary comparison.

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

• Change in Fasting Plasma Glucose (FPG) Concentration
• Change in Plasma Glucagon Concentration
• Change in Plasma Insulin Concentration

9. Statistical Interpretation

10. Statistical Methods Explained

Continuous outcomes are presented as means with standard errors. A mean gives the central value of a group’s measurements, while the standard error describes the precision of that estimated mean. It is not a standard deviation and should not be read as the typical spread among individual participants. The registry does not post the underlying participant-level data, so the distribution of responses cannot be assessed from these summaries alone.

What does a mean difference represent?

A mean difference compares the reported group mean for one treatment with the reported mean for its reference group. In the primary comparisons, placebo is the reference. A negative estimate means the treatment group’s reported change is lower than the placebo group’s reported change on the recorded scale; a positive estimate means it is higher. Direction alone does not establish clinical importance. Interpretation also depends on the endpoint, the measurement timeframe, and the uncertainty around the estimate.

The comparison estimates and confidence intervals posted alongside the means are recalculated, unadjusted summaries. They use the group means, standard errors, and sample sizes in the registry record. They are not adjusted for baseline values, additional participant characteristics, or other outcomes. Since no study-team analysis is listed for the outcomes, the recalculated comparisons should be distinguished from a prespecified trial analysis. The discrepancy flag is false, so there is no stated conflict with a sponsor analysis that would take precedence.

Why does an interval matter?

A confidence interval gives a range of effect estimates compatible with the data under the calculation’s assumptions. It communicates uncertainty more directly than a point estimate alone. When an interval for a mean difference includes zero, the posted data are compatible with no group difference as well as with differences in either direction at the interval’s limits. When it excludes zero, the interval indicates that the unadjusted estimate is less compatible with a zero difference under that calculation. Neither situation establishes clinical importance, and an interval does not guarantee that the true effect lies within its endpoints.

The posted p-values are unadjusted. A p-value measures how unusual the observed data would be under a specified null model, given the assumptions used for the calculation. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The p-values do not incorporate adjustment for multiple comparisons or a reported trial-specific model. No adjustment method is reported in the registry record.

What is the role of the design information?

Randomization is listed, and the design is parallel-group, meaning the posted summaries correspond to distinct treatment groups rather than repeated treatment periods within the same participants. The registry lists no masking. Those details describe broad design features, but they do not establish the details of randomization implementation, concealment, or measurement procedures beyond the endpoint description. These details are not reported in the registry record.

The outcome description says the acute EGP measurement followed an overnight fast and used tracer infusion. It also describes administration of one dose of placebo, exenatide, dapagliflozin, or both after the equilibration period. The posted primary timeframe is acute exposure. Although the endpoint title refers to an additional assessment after 16 weeks, no separate 16-week primary result is posted. The secondary outcome summaries do have a 16-week timeframe for fasting plasma glucose and a baseline-to-16-week timeframe for glucagon and insulin.

For the secondary outcomes, the listed group means and the recalculated comparisons are also unadjusted. The registry gives no reported analyses for these outcomes. The fasting plasma glucose comparison uses exenatide as its stated reference, and the glucagon and insulin summaries use the combination group as their stated reference. These are not identical comparison structures to the primary placebo-referenced results, so estimates should be interpreted within their own outcome rather than treated as direct replications of the primary contrast.

Why can over-dispersion matter in general?

In general, over-dispersion means observed variability is greater than a statistical model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow; if it accounts for too much variability, the reverse may occur. This is a general statistical consideration, not a reported feature of this trial. The record does not report a model assessment for over-dispersion, and the continuous summaries do not provide enough information to assess the shape of individual participant data.

Likewise, missing-data methods, analysis populations, covariate adjustment, and sensitivity analyses are not reported in the registry record. It is not possible to determine from the posted summaries whether all randomized participants contributed to every outcome, how missing measurements were handled, or whether the analysis followed an intention-to-treat approach. These omissions matter because analysis choices can affect estimates and their uncertainty, especially when outcome data are incomplete.

11. Confidence Intervals and Precision

Precision is conveyed by the standard errors and confidence intervals, rather than by the point estimates alone. The primary group means are reported with standard errors, and the recalculated comparisons include confidence intervals. For exenatide versus placebo and dapagliflozin versus placebo, the intervals do not include zero and the unadjusted p-values are each p < 0.001. For the combination versus placebo, the interval includes zero and the unadjusted p-value is 0.166. This distinction describes statistical uncertainty in these unadjusted comparisons; it does not establish whether an estimated difference is large enough to matter clinically.

Group sizes for the posted primary summaries are 25 for each active-treatment group and 15 for placebo. The smaller placebo group contributes less information to each placebo-referenced comparison than a larger group would, all else equal. This is a general precision principle, not a new calculation of the study’s uncertainty. The standard errors also differ between groups, and the record does not provide participant-level distributions from which to check the assumptions behind the recalculated intervals.

Confidence intervals are more informative than a threshold-only interpretation because they show a range of values consistent with the observed summaries under the calculation’s assumptions. But the recalculated intervals are unadjusted and do not reflect multiplicity, covariate adjustment, or any trial-specific model that is not reported in the registry record. Their precision is therefore conditional on the simple comparison approach. The posted primary results are acute; no confidence interval for a distinct 16-week primary EGP result is reported in the registry record.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size planning figures are participants per arm, not a total across the trial. They are illustrations based on the observed effect in each comparison, not a description of the trial’s original design assumptions. The stated calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios consider detecting 100%, 75%, or 50% of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column means the number of participants per arm that the stated planning calculation estimates would be needed for an 80% chance of detecting the specified effect under the calculation’s assumptions, if that effect were real. The 90% power column uses the same interpretation with a higher target chance of detection. These are planning quantities, not observed properties of the completed trial. This is not observed power.

Smaller effects require more participants under these assumptions. The planning figures therefore increase when the target effect is reduced from the observed effect to a fraction of it. The estimates are especially sensitive when an observed effect is small relative to its uncertainty, as can happen with a modest estimated difference. They should not be read as evidence that the trial was designed to detect the observed result or that a particular comparison has been adequately powered. The registry record does not report the study team’s original assumptions, planned primary contrast, or any adjustment for multiple comparisons.

The calculation is a simplified two-group illustration. It does not account for details not included in the stated assumptions, such as missing observations, unequal group allocation in the posted outcome summaries, or a different analysis model. The planning numbers are useful for illustrating how a target effect and desired power relate to per-arm sample size, but they are not a substitute for the trial’s design documentation.

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 = -0.150; pooled standard deviation σ = 0.092.
2. n = 2 × (1.96 + 0.842)² × 0.092² / -0.150² = 5.9, rounded up to 6 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 <- -0.15                      # observed difference in means
sigma <- 0.0923380516876639                     # 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(2981069)
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 = 6 (80% power), 8 (90% power)
 75% of observed effect: n per arm = 11 (80% power), 15 (90% power)
 50% of observed effect: n per arm = 24 (80% power), 32 (90% power)
power.t.test: 7.1 
Simulated power at n = 6 per arm: 0.719 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and three secondary outcomes, with multiple treatment comparisons represented in the posted summaries. Testing several outcomes or contrasts increases the chance that at least one result will appear statistically notable by chance, even when each individual test uses the same nominal threshold. This is the general multiplicity problem. The registry record does not report a correction procedure, a hierarchy for testing outcomes, or a plan identifying which secondary comparisons were confirmatory. The reported p-values are unadjusted and should be interpreted accordingly.

Missing-data methods and analysis populations are also not reported in the registry record. The outcome summaries include group-specific sample sizes, but there is no participant flow information describing how those counts relate to enrollment, randomization, discontinuation, or missing measurements. The record does not state whether analyses used all randomized participants, only participants with available outcome data, or another population. It also does not report imputation, sensitivity analyses, or reasons for missing outcomes.

These omissions make it difficult to judge whether the reported summaries could be affected by selective availability of measurements. They also prevent assessment of whether the simple unadjusted calculations align with the intended trial analysis. The record does not report an interim-analysis plan or stopping rules; no assumptions about interim monitoring can be made from the posted information.

Randomization is stated, but details of sequence generation and allocation concealment are not reported in the registry record. Masking is listed as none. These features should be distinguished: a randomized design can reduce confounding in expectation, while lack of masking may affect behavior, measurement, or reporting depending on the outcome and procedures. The registry does not provide enough information to determine whether such effects occurred. Together, these reporting gaps limit the strength of conclusions that can be drawn from nominal significance results.

15. 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 non-serious adverse event terms

The posted serious adverse event counts are zero participants affected in each of the four groups. The numbers at risk are 25 in each active-treatment group and 15 in the placebo group. The record also lists zero deaths in every group, and no serious adverse event terms are listed. These are the registry’s reported counts; they do not establish that no event could have occurred outside the recorded period or under a different definition.

Other adverse events are listed for the three active-treatment groups, while the placebo group has zero affected participants in that category. These counts are separate from the serious-event counts and should not be combined with them. The registry record does not provide the event terms, severity grades, timing, relatedness assessments, or a detailed collection method. Without those details, the counts cannot characterize the types or clinical importance of the events, and comparisons across groups should remain descriptive.

The different group sizes also matter when reading raw counts: a count is not a rate and does not by itself account for how many participants were at risk. No additional rate calculation is made. The safety information is limited to the posted participant counts and does not support a broader assessment of comparative safety.

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

The results describe mean changes in measured physiological outcomes in the posted groups. For the primary endpoint, the registry provides acute EGP summaries after single-dose exposure and recalculated unadjusted comparisons with placebo. Those results identify differences in the posted acute means for exenatide and dapagliflozin, while the combination comparison has an interval that includes zero. The estimates should be interpreted with their uncertainty and with the fact that the comparisons are not reported analyses from the study team.

These data do not establish what happens to EGP after 16 weeks. Although the primary outcome title mentions both acute exposure and a further measurement after 16 weeks of treatment, a separate 16-week primary result is not reported in the registry record. The secondary outcomes provide some 16-week information for fasting plasma glucose, glucagon, and insulin, but they are not substitutes for the missing later EGP result.

Statistical evidence is not the same as clinical importance. The registry does not state a threshold for a meaningful EGP change or link the reported changes to clinical outcomes. Nor do group means show the range of individual responses. The posted comparisons cannot establish a biological mechanism, explain why groups differ, or determine whether differences persist beyond the measurement timeframes.

The randomized design is relevant to how comparisons are interpreted, but design details and the full analysis plan are not reported. The absence of masking, unadjusted recalculations, unreported missing-data methods, and multiple outcomes all temper inference. The data are best read as registry-posted descriptive summaries and simple comparisons, not as a complete account of the trial’s planned statistical analysis or as a basis for medical decisions.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it puts several physiological measures and treatment groups into a randomized parallel design, while the registry’s posted primary result is an acute measurement. The distinction between an acute response and a response after a course of treatment is central: an estimate from a single-dose exposure addresses a different timeframe from a later treatment assessment. The primary outcome title includes both, but only the acute timeframe has posted results.

The record also illustrates why estimates, uncertainty, and analysis provenance need to be read together. The group means and standard errors make the outcome scale visible, and the confidence intervals show how uncertain the unadjusted contrasts are. The recalculated comparisons offer a consistent way to describe differences from posted summaries, but they are not the study team’s reported analyses. The lack of reported analyses means the registry does not establish whether these comparisons match the original prespecified approach.

Finally, the secondary outcomes show the interpretive challenge of many related measures: they can add context, but multiple unadjusted tests do not carry the same weight as a single clearly specified confirmatory analysis. The missing multiplicity plan, analysis-population details, and separate later primary result make transparent reporting especially important. Readers can distinguish what the posted summaries say from what remains unknown without turning physiological estimates into claims about treatment benefit.

18. Limitations

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

Several limitations are specific to the available registry record. The primary endpoint title refers to acute exposure and an additional assessment after 16 weeks, but the posted primary timeframe and results are acute. A later primary EGP estimate is not reported in the registry record, so the primary summaries cannot describe the full time course implied by the title.

The acute outcome description says that 20 subjects per group would receive study medication, while the posted primary outcome counts are 25, 25, 25, and 15. The record does not explain this difference. It also does not provide a participant flow account or clarify the relationship between the enrollment figure and outcome-specific counts. This limits interpretation of how the posted analysis set was assembled.

There are no reported analyses for the primary or secondary outcomes. The comparisons discussed are simple unadjusted recalculations based on group summaries, rather than a reported model that could account for baseline values or other covariates. Missing-data procedures, analysis populations, protocol deviations, adherence, and sensitivity analyses are not reported in the registry record.

Additional limitations include the absence of a reported multiplicity strategy, a detailed randomization and allocation-concealment description, and masking. The registry also does not post participant-level outcome distributions, making it impossible to inspect outliers or the shape of responses. Finally, safety information is limited to counts without event terms or severity details. These limitations constrain precision and interpretation; they do not by themselves establish that the trial methods were inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effect of Chronic Exenatide Therapy on Beta Cell Function and Insulin Sensitivity in T2DM — NCT02981069.
• Registry record last updated 2023-07-20; status last verified 2023-06.
• Results first posted 2023-07-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed, randomized, unmasked, parallel-group phase 4 study in type 2 diabetes, with enrollment of 90. The primary outcome is change in endogenous glucose production. Four groups are represented in the posted primary summaries: exenatide, dapagliflozin, their combination, and placebo. The posted primary timeframe is acute exposure after a single dose, while a separate result after 16 weeks is not reported in the registry record.

The registry also posts secondary summaries for fasting plasma glucose, glucagon, and insulin. Comparison estimates and p-values discussed are unadjusted recalculations; no study-team analyses are listed. Serious adverse events and deaths are recorded as zero in each group, with other adverse event counts also posted. Multiplicity methods, missing-data handling, analysis populations, and detailed safety-event descriptions are not reported in the registry record.