A Comparison of Adding Exenatide With Switching to Exenatide in Patients With Type 2 Diabetes Experiencing Inadequate Glycemic Control With Sitagliptin Plus Metformin: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Comparison of Adding Exenatide With Switching to Exenatide in Patients With Type 2 Diabetes Experiencing Inadequate Glycemic Control With Sitagliptin Plus Metformin (NCT00870194), a randomized phase 4 study. The primary outcome is Change in HbA1c (Percent).

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, parallel-group phase 4 trial, recorded as completed. The registry lists enrollment as 255. The study compared two treatment strategies for people with type 2 diabetes whose glycemic control was inadequate on sitagliptin plus metformin: add exenatide while continuing sitagliptin, or stop sitagliptin and switch to exenatide while continuing metformin. The arm names are Exenatide + Sitagliptin and Exenatide + Placebo.

The primary endpoint was change in HbA1c from baseline to Week 20. Its analysis population was the Per Protocol Set, as defined in the registry record. The posted arm summaries for this endpoint include 97 participants in the Exenatide + Placebo arm and 111 in the Exenatide + Sitagliptin arm. Those endpoint analysis counts are not the same as the overall enrollment figure, and the record also reports different numbers at risk for safety outcomes. The reasons for those differences are not reported in the registry record.

Randomization is intended to allocate participants among treatment groups in a way that limits systematic differences at study entry. Masking is intended to reduce the influence of treatment knowledge on participant experience, care, and assessment. A parallel-group design assigns participants to one strategy rather than having each participant receive both strategies in sequence. These are general features of the design; details of the allocation procedure, masking implementation, and any safeguards are not reported in the registry record.

The registry lists the study as phase 4 and reports 255 enrolled participants. The original sample-size assumptions, justification for the chosen enrollment, planned interim analyses, and full statistical analysis plan are not reported in the registry record. The sample-size illustrations accompanying the results are based on observed effects and should not be read as the trial's original design calculations.

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: Per Protocol Set: the set of data generated by the subset of patients who sufficiently complied with the protocol to ensure that these data would be likely to exhibit the effects of treatment, according to the underlying scientific model.

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 (Percent), measured over Baseline to 20 Weeks.

The primary endpoint was change in HbA1c, expressed as a percentage, from baseline to Week 20. HbA1c reflects average blood glucose over a period of time and is commonly used in diabetes trials as a measure of glycemic control. This makes it relevant to a study asking whether changing or adding a glucose-lowering treatment strategy is associated with a difference in glycemic outcomes. This is general context for the measure, not a claim about the clinical importance of any particular result in this trial.

The registry describes the primary measure as a least-squares mean, with standard error as its dispersion measure. A least-squares mean is a model-based estimate of a group mean; unlike a simple arithmetic mean, it can incorporate the model structure and adjustments used in the analysis. The posted record specifies a per-protocol analysis population and a baseline-to-Week-20 timeframe. It does not give the full model specification or list the covariates used in the primary analysis, so those details are not reported in the registry record.

Change scores express how the measure moved relative to baseline. Negative values in the posted arm summaries indicate reductions in HbA1c over the measurement interval. The comparison between groups is important because a change within one group alone does not show whether outcomes differed between treatment strategies. The registry's own repeated-measures analysis and the recalculation from posted summaries address that between-group contrast using different approaches.

7. Results Posted in the Registry

• Exenatide + Sitagliptin: mean -0.68 versus -0.38 on control; difference -0.30 (95% CI -0.54 to -0.06), standardized effect d = -0.35; z-test p = 0.013.

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 FSG (mmol/L)

• 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 + Sitagliptin: mean -0.55 versus 0.06 on control; difference -0.61 (95% CI -1.22 to 0.00), standardized effect d = -0.28; z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exenatide + Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

Change in Body Weight (kg)

• 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 + Sitagliptin: mean -2.20 versus -2.58 on control; difference 0.38 (95% CI -0.30 to 1.06), standardized effect d = 0.15; z-test p = 0.273.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exenatide + Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

Change in Waist Circumference (cm)

• 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 + Sitagliptin: mean -2.36 versus -3.25 on control; difference 0.89 (95% CI -0.18 to 1.96), standardized effect d = 0.23; z-test p = 0.102.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exenatide + Sitagliptin and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend beyond HbA1c to include glucose, body weight, waist circumference, waist-to-hip ratio, self-monitoring blood glucose, and the proportions meeting specified HbA1c thresholds. The registry lists 16 posted secondary outcomes, but outcome-level results are not available in the record for every listed measure. Results for the listed HbA1c threshold outcomes and several other measures are not reported in the registry record, so a complete secondary-outcome pattern cannot be established from the available results.

For the continuous secondary results with posted arm summaries, the directions are not uniform. Fasting serum glucose change is numerically more favorable in the Exenatide + Sitagliptin arm, while the mean changes in body weight and waist circumference are numerically more negative in the Exenatide + Placebo arm. The registry also reports sponsor analyses for these outcomes. This variation is compatible with secondary measures capturing different aspects of the treatment strategies; it does not, by itself, establish a coherent overall advantage for either approach.

The primary outcome remains the central result for the trial question. Secondary endpoints can add context, but their evidence is harder to interpret when multiple outcomes are assessed. If many comparisons are tested, some may appear notable by chance even when there is no corresponding underlying difference. In general, adjustment for multiplicity or a prespecified hierarchy can help control that risk. The multiplicity strategy and complete testing hierarchy are not reported in the registry record. The secondary findings should therefore be treated as supportive or exploratory rather than as independent confirmation of the primary conclusion.

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

• Percentage of Patients Achieving HbA1c <=7.0%
• Percentage of Patients Achieving HbA1c <7.0%
• Percentage of Patients Achieving HbA1c <=6.5%
• Change in FSG (mmol/L)
• Change in Body Weight (kg)
• Change in Waist Circumference (cm)
• Waist-to-Hip Ratio
• SMBG (mmol/L)

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the study's reported analysis from the simple recalculation based on arm summaries. The registry reports a primary Mixed Model Repeated Measures analysis and also gives group-level least-squares means with standard errors. The recalculated contrast uses the posted summary statistics and is an unadjusted comparison. These methods answer related questions, but their estimates and uncertainty need not match exactly.

What does a least-squares mean represent?

A least-squares mean is an estimate generated by a statistical model. In general, a model can account for repeated observations and other specified features of the data. This differs from simply averaging all observed values. The registry identifies the primary parameter as a least-squares mean and gives a Mixed Model Repeated Measures analysis, but the full model formula, included covariates, handling of baseline values, and covariance structure are not reported in the registry record. Without those details, the sponsor's estimate cannot be reconstructed from the short result listing.

The primary arm summaries report standard errors rather than standard deviations. A standard error describes uncertainty in an estimated mean; it is not a measure of the spread of individual participants' measurements. The recalculation derives an approximate pooled standard deviation from those standard errors and sample sizes in order to form an unadjusted standardized comparison. Because this is an approximation based on summary data, it should be treated as a descriptive re-analysis rather than as the trial's model-based inference.

Why are the p-values different?

The registry reports p = .012 for the sponsor's repeated-measures analysis, while the unadjusted recalculation gives p = 0.013. The recalculation uses a different statistical construction and does not reproduce the repeated observations or model adjustments used by the sponsor. Small differences in estimates, standard errors, and p-values can follow from these methodological differences. The record does not report evidence of a discrepancy between the sponsor result and the recalculation; nevertheless, the sponsor's prespecified analysis is the primary reference for the trial's own inference.

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Interpreting a p-value also depends on the analysis being planned and on how many outcomes or analyses were examined. The registry does not report the full testing hierarchy or multiplicity procedure.

What does non-inferiority require?

In general, a non-inferiority analysis asks whether an intervention is not worse than a comparator by more than a prespecified margin. The margin defines the largest difference that would still be considered compatible with non-inferiority under the study's framework. This is different from testing whether two means are exactly equal. The registry categorizes the sponsor's primary result as non-inferiority or equivalence and reports a model-based contrast, but it does not report the margin or the detailed decision rule. Accordingly, the category and p-value alone are not enough to independently verify the non-inferiority conclusion.

The sign of a treatment difference depends on subtraction order. The recalculation reports Exenatide + Sitagliptin minus Exenatide + Placebo, producing an estimate of -0.3. The sponsor reports a positive least-square mean difference of 0.30, consistent with the reverse contrast. These signs describe the same ordering issue rather than contradictory directions. Any interpretation should state which arm is subtracted from which.

Why does the analysis population matter?

The registry defines the primary analysis population as the Per Protocol Set. In general, per-protocol analyses include participants considered sufficiently compliant with the protocol. This population can be useful for questions about outcomes under adherence to the assigned regimen, but excluding or omitting participants after randomization can affect the protection offered by random allocation. The registry does not report the number excluded from this analysis, the reasons for exclusions, or a corresponding intention-to-treat primary estimate. Those details are not reported in the registry record.

Repeated-measures models can use measurements collected at multiple time points and can account for within-participant correlation. In general, such models require assumptions about the outcome structure and about missing observations. The registry does not give the measurement schedule beyond the baseline-to-Week-20 endpoint timeframe or specify the missing-data assumptions and sensitivity analyses. The presence of a model name should therefore not be mistaken for a complete description of the analysis.

Finally, a confidence interval communicates a range of estimates compatible with the data and analysis assumptions. It is useful alongside a p-value because it shows the direction and precision of the estimated contrast. The sponsor's interval is model-based, while the recalculated interval follows from the unadjusted summary-statistic approach. They should be read as results from distinct analyses rather than combined into a single interval.

11. Confidence Intervals and Precision

The recalculated primary contrast is -0.3 percentage points, with a 95% confidence interval from -0.536 to -0.064. This interval is for Exenatide + Sitagliptin minus Exenatide + Placebo. Its negative values indicate that the estimate favors a larger HbA1c reduction in the first arm under this subtraction order. The interval does not include zero, but it still spans a range of possible differences, so the point estimate should not be treated as exact.

A confidence interval is a range produced by a statistical procedure that, under its assumptions, would cover the underlying parameter in a stated proportion of repeated applications. It is not a statement that there is a 95% probability that this particular interval contains the true value. Its width reflects both the observed data and the analysis method. Here, the recalculated interval reflects an unadjusted approach based on posted summary statistics, whereas the sponsor reports a model-based 95% interval from 0.07 to 0.53 for the reverse contrast.

The numerical difference between the intervals should be interpreted in light of their distinct methods and subtraction orders. The record does not report the full model specification needed to assess every source of that difference. Nor does it report the non-inferiority margin needed to judge whether the model-based interval satisfies the study's stated non-inferiority question. Precision about the estimated contrast is not the same as certainty about the clinical importance of the result.

Standard errors in the arm summaries describe uncertainty in the estimated group means, not the range of individual participant outcomes. The analysis counts also matter to precision, but the registry does not report a complete account of missing observations or exclusions. These limitations make the reported intervals useful summaries of uncertainty, while leaving important aspects of the analysis assumptions unresolved.

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 illustrations are planning calculations based on the observed effect, not the trial's original design assumptions. For these continuous outcomes, the figures are participants per arm, rather than total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial's own sample-size justification and original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding number for a 90% chance. These are design-planning probabilities under a hypothetical repeated-sampling framework, not guarantees about what a particular study will find. The values are not observed power.

The rows for 100%, 75%, and 50% of the observed effect ask how the required group size changes if the effect worth detecting is the full observed estimate or a smaller fraction of it. When the effect to detect is smaller, more participants are generally needed to distinguish it from random variation. The planning figures should be interpreted as illustrations rather than as recommendations or evidence that the completed trial was adequately or inadequately sized. They also do not account for design details that are absent from the registry record, such as the original assumptions used to plan enrollment or possible adjustments in the sponsor's model.

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 = -0.300; pooled standard deviation σ = 0.863.
2. n = 2 × (1.96 + 0.842)² × 0.863² / -0.300² = 130.0, rounded up to 131 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 <- -0.3                      # observed difference in means
sigma <- 0.863418358697522                     # 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(870194)
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 = 131 (80% power), 175 (90% power)
 75% of observed effect: n per arm = 232 (80% power), 310 (90% power)
 50% of observed effect: n per arm = 521 (80% power), 697 (90% power)
power.t.test: 131 
Simulated power at n = 131 per arm: 0.800 (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's primary result is a Mixed Model Repeated Measures analysis in the Per Protocol Set. It reports a least-square mean difference of 0.30, a 95% confidence interval from 0.07 to 0.53, and p = .012. The result is categorized in the registry as a non-inferiority or equivalence analysis. The contrast is presented in the opposite direction from the recalculation, which defines the difference as Exenatide + Sitagliptin minus Exenatide + Placebo and reports -0.3 with a 95% confidence interval from -0.536 to -0.064.

The recalculation is a simple unadjusted re-analysis of posted arm summaries. It does not reproduce the sponsor's repeated-measures model, its analysis population details beyond the primary set description, or any adjustments in that model. Its p-value is 0.013, compared with the sponsor's p = .012. Such small differences are consistent with use of different analysis methods, and the registry does not identify a discrepancy between the results.

The sponsor's analysis is the appropriate reference for the trial's reported inference; the recalculation is supplementary and helps readers inspect the contrast using the posted summaries. The registry record does not report the non-inferiority margin or detailed decision criteria. Therefore, the sponsor's label and p-value cannot by themselves establish how the prespecified non-inferiority rule was applied or independently confirm that it was met.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several outcomes, time points, treatment contrasts, or analysis populations. In general, the more statistical tests considered, the greater the chance that at least one result will appear noteworthy by chance alone. This is why confirmatory trials often specify a primary endpoint and a testing hierarchy or adjustment procedure in advance. The registry identifies change in HbA1c as the primary outcome and lists multiple secondary outcomes, but the multiplicity procedure and full hierarchy are not reported in the registry record.

The result listing includes 17 outcome measures and 18 analyses. Those counts indicate that more than one result or analysis was posted, but do not reveal which tests were prespecified, which were exploratory, or whether a formal correction was applied. The unadjusted p-values for recalculated comparisons should not be interpreted as multiplicity-adjusted evidence. The sponsor's primary result is described as a non-inferiority or equivalence analysis, but the detailed analysis plan, margin, and decision rule are not reported in the registry record.

Missing-data handling is also important, particularly for a repeated-measures analysis. In general, the validity of model-based estimates may depend on assumptions about why observations are missing and how the model uses available measurements. The record specifies a baseline-to-Week-20 timeframe and names a Mixed Model Repeated Measures method, but the missing-data assumptions, imputation procedures, sensitivity analyses, and participant flow through the analysis are not reported in the registry record.

The primary population is described as the Per Protocol Set, with a definition based on sufficient protocol compliance. The number of participants in the primary analysis differs from overall enrollment, and safety counts differ from the primary endpoint counts. The reasons for these differences, the precise exclusions from the per-protocol population, and an intention-to-treat analysis are not reported in the registry record. These omissions limit assessment of how post-randomization exclusions and incomplete data may affect interpretation.

Interim analyses, stopping rules, the original sample-size justification, and the full statistical analysis plan are not reported in the registry record. Their absence does not show that such procedures were or were not used; it means the record does not permit their assessment. For that reason, the posted estimates and p-values should be read with the reported analysis labels, while recognizing that several prespecification and robustness details remain unavailable.

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: arthralgia (0.8%), back pain (0.8%), hypoglycaemia (0.8%), lumbar hernia (0.8%), lumbar spinal stenosis (0.8%).

The safety summaries report serious adverse events in 4 of 127 participants at risk in the Exenatide + Placebo group and 6 of 128 participants at risk in the Exenatide + Sitagliptin group. The record also lists other adverse events in 36 of 127 and 28 of 128 participants, respectively. These counts describe the posted safety groups; they are not the same denominators as those in the primary per-protocol endpoint summaries.

The registry lists arthralgia, back pain, hypoglycaemia, lumbar hernia, lumbar spinal stenosis, and urticaria among the serious adverse event terms, each reported as 0.8%. The record does not give further detail in the information available for this analysis about event timing, severity beyond the serious classification, or the relationship of each event to treatment. Death counts are not reported in the registry record.

These figures are descriptive. Comparing event counts across groups does not by itself establish that a treatment caused an event or that one strategy has a different safety profile. The groups at risk and the posted event categories should be kept in view when reading the counts, and the record does not provide enough detail to support a broader safety conclusion.

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

The primary summaries show a larger mean reduction in HbA1c in the Exenatide + Sitagliptin arm than in the Exenatide + Placebo arm over baseline to Week 20. The unadjusted recalculation estimates the difference as -0.3 percentage points when subtracting the placebo arm from the sitagliptin arm. The sponsor's model-based result reports a positive 0.30 contrast in the reverse order. The two presentations point in the same direction once their subtraction orders are taken into account.

The registry categorizes the sponsor's primary analysis as non-inferiority or equivalence, but it does not report the margin or detailed decision rule. A reader therefore cannot verify from the posted information alone whether the trial met its prespecified non-inferiority criterion. The observed difference and its confidence interval describe the data under the reported analyses; neither a p-value nor a direction of difference is a complete substitute for the missing design criterion.

The result does not show that the treatment strategies are identical. Nor does the recalculated difference alone establish that one strategy is clinically preferable. Statistical estimates describe average outcomes in the analyzed population and carry uncertainty. Clinical importance depends on context and prespecified criteria that are not reported in the registry record. The per-protocol analysis also does not, by itself, answer how results would compare under an analysis including all randomized participants.

Secondary results vary in direction, and complete results and multiplicity details are not reported for every listed outcome. Safety counts are descriptive and do not establish causation. Generalization beyond the trial population should be cautious because the registry record does not provide a full account of eligibility criteria, participant characteristics, or all analysis details. These findings should be understood as statistical evidence from a particular randomized trial, not as medical advice or a definitive statement about treatment for an individual.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it compares two strategies that share exenatide and metformin but differ in whether sitagliptin is continued or replaced. The question is therefore about the incremental strategy contrast, not simply about exenatide versus no exenatide. The randomized, double-masked, parallel-group design is relevant to that comparison, while the per-protocol primary population raises questions about how the analysis relates to the original randomized groups.

It also illustrates why non-inferiority claims require more than a small p-value or a confidence interval that excludes zero. Non-inferiority depends on a prespecified margin and a decision rule that give meaning to the interval in relation to an acceptable difference. The registry labels the primary analysis as non-inferiority or equivalence, but the margin and detailed rule are not reported. That gap matters because the central clinical question is framed as whether switching is non-inferior to adding treatment.

The record also demonstrates how analysis choices shape reported contrasts. The sponsor's repeated-measures model and the unadjusted recalculation use different approaches and report the difference in opposite directions. Recognizing subtraction order avoids mistaking sign changes for conflicting results; recognizing model differences avoids treating the recalculation as a reproduction of the sponsor's inference.

Finally, the multiple secondary outcomes and incomplete reporting of their results highlight the importance of prespecified outcome hierarchies and transparent multiplicity handling. Sample-size illustrations based on observed effects can help readers understand planning trade-offs, but they do not recover the study's original design rationale. Together, these points make the registry a useful example of interpreting statistical claims while separating what is reported from what remains unknown.

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.

Several trial-specific limitations arise from details missing in the registry record. The non-inferiority margin and decision rule are not reported, even though the sponsor's primary analysis is categorized as non-inferiority or equivalence. This prevents an independent assessment of the defining criterion for that question. The full statistical analysis plan, original sample-size justification, and any interim analyses or stopping rules are also not reported.

The primary analysis uses the Per Protocol Set. The registry's definition refers to sufficient compliance, but the participant flow, reasons for exclusion, number excluded, and corresponding intention-to-treat result are not reported. Because the primary endpoint counts are not the same as total enrollment, the lack of detail on missing outcomes and exclusions limits assessment of how the analyzed subset relates to randomization.

The sponsor's Mixed Model Repeated Measures result is not fully specified. Covariates, model structure, repeated-measure covariance assumptions, handling of missing observations, and sensitivity analyses are not reported in the registry record. The unadjusted recalculation uses posted summaries and cannot substitute for those details.

Multiplicity procedures are not reported despite multiple posted outcomes and analyses. Results are also not reported for every listed secondary outcome. This limits the strength of conclusions that can be drawn from the secondary findings and makes it difficult to distinguish confirmatory from exploratory testing. Safety information is summarized as counts and selected serious-event terms; further detail about event timing, treatment attribution, and deaths is not reported in the registry record.

Finally, the registry information available for this analysis does not give a full description of participant characteristics or all eligibility criteria. The findings therefore have limits in how confidently they can be generalized to populations beyond those studied.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Comparison of Adding Exenatide With Switching to Exenatide in Patients With Type 2 Diabetes Experiencing Inadequate Glycemic Control With Sitagliptin Plus Metformin — NCT00870194.
• Registry record last updated 2015-04-09; status last verified 2015-03.
• Results first posted 2011-06-17.
• 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

NCT00870194 is a completed, randomized, double-masked, parallel-group phase 4 study with reported enrollment of 255. It compared adding exenatide to sitagliptin plus metformin with stopping sitagliptin and switching to exenatide while continuing metformin. The primary endpoint was change in HbA1c from baseline to Week 20 in the Per Protocol Set.

The sponsor's Mixed Model Repeated Measures analysis reports a least-square mean difference of 0.30, a 95% confidence interval from 0.07 to 0.53, and p = .012, with the result categorized as non-inferiority or equivalence. A recalculation from posted summaries gives -0.3 for Exenatide + Sitagliptin minus Exenatide + Placebo, with a 95% confidence interval from -0.536 to -0.064 and p = 0.013. The contrast directions are reversed. The non-inferiority margin, full analysis plan, multiplicity handling, and important missing-data details are not reported in the registry record.