This page provides an independent statistical analysis and educational interpretation of publicly reported results. ClinicalTrials.gov provides the official trial registry record. Numerical trial results on this page are restricted to the results posted in the ClinicalTrials.gov record; calculations added by Clinical Biostats are labelled as such.
1. Trial at a Glance
This page covers the registry results for Study to Evaluate the Safety and Efficacy of the Addition of Omarigliptin (MK-3102) Compared With the Addition of Sitagliptin in Participants With Type 2 Diabetes Mellitus With Inadequate Glycemic Control on Metformin (MK-3102-026) (NCT01841697), a randomized phase 3 study. The primary outcome is Change From Baseline in A1C at Week 24.
| Feature | Registry value |
|---|---|
| ClinicalTrials.gov identifier | NCT01841697 |
| Phase | Phase 3 |
| Condition | Type 2 Diabetes |
| Allocation | Randomized |
| Design model | Parallel |
| Masking | Double |
| Enrollment | 642 |
| Arms in the primary outcome | 2 |
| Lead sponsor | Merck Sharp & Dohme LLC |
| Results posted | Yes |
2. Clinical Question
Population
Participants had type 2 diabetes with inadequate glycemic control on metformin. The registry describes a full analysis set comprising randomized participants who received at least one dose and had a baseline or qualifying post-randomization measurement for the endpoint.
Intervention
Omarigliptin 25 mg once weekly was added to a stable pre-study metformin dose. Participants could receive glimepiride as rescue therapy. The treatment period described for this arm was 24 weeks.
Comparator
Sitagliptin 100 mg once daily was added to a stable pre-study metformin dose, with placebo to omarigliptin once weekly. Glimepiride could also be used as rescue therapy in this arm.
Primary question
The stated primary hypothesis asked whether mean change from baseline in A1C after 24 weeks with omarigliptin was non-inferior to mean change with sitagliptin. The registry reports the treatment contrast and its confidence interval, but the non-inferiority margin is not reported in the registry record.
The study concerns the comparative addition of two drugs for participants whose glycemic control on metformin was considered inadequate. The primary outcome was continuous: change in A1C from baseline to Week 24, expressed as a percentage and estimated using least squares means. The clinical question is therefore not simply whether either arm changed from baseline, but how the mean change differed between the randomized groups and how precisely that contrast was estimated.
The record also describes secondary questions about fasting plasma glucose and the proportions of participants reaching A1C goals. Those outcomes provide additional perspectives, but they do not replace the primary comparison. The principal interpretive constraint is that a non-inferiority conclusion depends on a prespecified margin. Because that margin is not reported in the registry record, the posted contrast cannot by itself establish whether the stated criterion was met.
3. Trial Design
The registry identifies this as a phase III, multicenter, double-blind, randomized, parallel-group study. Enrollment was 642. The study status is completed. The stated population had type 2 diabetes with inadequate glycemic control while taking metformin. Participants were assigned to add either omarigliptin or sitagliptin to their metformin treatment.
The omarigliptin regimen was 25 mg once weekly, with placebo to sitagliptin once daily. The sitagliptin regimen was 100 mg once daily, with placebo to omarigliptin once weekly. This double-dummy approach is consistent with the listed placebo interventions and allows the dosing schedules to be masked. Participants continued their stable pre-study metformin dose; the arm descriptions state a total daily dose of at least 1500 mg. Glimepiride, at a stated daily dose of 1–6 mg, could be used as rescue therapy.
The brief summary describes a 2-week run-in with placebo plus metformin before the double-blind treatment period. The primary comparison was assessed at Week 24, and the record gives baseline and Week 24 as the primary endpoint timeframe. The arm descriptions also specify 24 weeks of assigned treatment. The registry lists 322.0 participants in the omarigliptin arm and 320.0 in the sitagliptin arm for the primary outcome.
Randomization and double blinding help limit allocation and assessment biases, but they do not establish that every possible source of bias was controlled. The registry record does not report the allocation ratio, the randomization sequence-generation details, or the procedures used to maintain concealment. It also does not provide enough information to reconstruct all treatment adherence, rescue-treatment, or follow-up procedures. These details should not be inferred from the study label or from the arm descriptions alone.
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
| Stage | Omarigliptin 25 mg Once Weekly | Sitagliptin 100 mg Once Daily |
|---|---|---|
| STARTED | 322 | 320 |
| COMPLETED | 302 | 302 |
| NOT COMPLETED | 20 | 18 |
Reasons for not completing this period:
| Reason | Omarigliptin 25 mg Once Weekly | Sitagliptin 100 mg Once Daily |
|---|---|---|
| Death | 0 | 1 |
| Lost to Follow-up | 4 | 1 |
| Withdrawal by Subject | 16 | 16 |
Analysis population for the primary outcome, as defined in the registry: Full analysis set population consists of all randomized participants who received at least one dose of study treatment and have a baseline measurement or a post-randomization measurement for the analysis endpoint subsequent to at least one dose of study treatment.
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.
| Characteristic | Unit | Omarigliptin 25 mg Once Weekly | Sitagliptin 100 mg Once Daily | Total |
|---|---|---|---|---|
| Participants analysed | 322 | 320 | 642 | |
| Age, Continuous | Years | 57.0 (SD 9.8) | 57.6 (SD 9.8) | 57.3 (SD 9.8) |
| Sex: Female, Male: Female | Participants | 171 | 145 | 316 |
| Sex: Female, Male: Male | Participants | 151 | 175 | 326 |
| Hemoglobin A1c (A1C) | Percent | 7.52 (SD 0.77) | 7.49 (SD 0.74) | 7.50 (SD 0.76) |
| Fasting plasma glucose (FPG) | mg/dL | 160.1 (SD 35.7) | 153.9 (SD 32.8) | 157.0 (SD 34.4) |
6. Primary Endpoint
The registry lists the primary outcome as Change From Baseline in A1C at Week 24, measured over Baseline and Week 24.
| Element | Registry entry |
|---|---|
| Result type | Least Squares Mean |
| Measure of spread | 95% Confidence Interval |
| Unit | Percent |
| Endpoint classification | Continuous Endpoint |
The primary endpoint was change from baseline in A1C at Week 24. The registry describes A1C as the percentage of glycated hemoglobin in whole blood, with samples collected at baseline and Week 24. The reported arm estimates are least squares mean changes, each accompanied by a 95% confidence interval.
A continuous change endpoint retains information about the size and direction of measured change rather than reducing each participant to a yes-or-no threshold category. For a comparison of two randomized groups, the treatment contrast in mean change is central: it indicates how far apart the estimated group means are, while its confidence interval conveys uncertainty around that contrast. This is a general explanation of the statistical role of a continuous endpoint; it does not establish how the model was specified in this study.
A1C was selected as the primary measure in the registry’s stated hypothesis about glycemic control. The endpoint description identifies the measurement and collection times but does not report a detailed laboratory method or the statistical model used to obtain the least squares means. The analysis population is defined in the record as randomized participants who received at least one dose and had a baseline or qualifying post-randomization measurement for the endpoint.
Because the stated objective was non-inferiority, interpretation requires more than noting whether the estimated contrast is close to zero. A non-inferiority margin defines the largest acceptable disadvantage under the prespecified framework. That margin, and the detailed decision rule, are not reported in the registry record.
7. Why No Re-analysis Is Shown
8. Statistical Interpretation
At Week 24, the least squares mean change in A1C was -0.47 in the omarigliptin arm and -0.43 in the sitagliptin arm. The reported difference in least squares means was -0.03, with a 95% confidence interval from -0.15 to 0.08. The point estimate is close to zero, while the interval includes zero and extends on both sides of it. Thus, the posted interval is compatible with a range of contrasts rather than identifying a single precise treatment difference.
The confidence interval is the key precision measure in this comparison. In general, a confidence interval describes the uncertainty associated with an estimate under the statistical procedure used; it is not a range containing a known proportion of individual participant outcomes. Here, the interval gives the registry’s reported uncertainty for the difference in least squares mean change. The registry does not report a p-value for this primary contrast, and none should be inferred from the other endpoints’ p-values.
The study’s stated primary hypothesis was non-inferiority. A point estimate near zero, or a confidence interval that includes zero, does not alone establish non-inferiority. The relevant comparison is between the confidence interval and the prespecified non-inferiority margin, together with the study’s analysis rules. The margin and those detailed rules are not reported in the registry record. Therefore, the reported contrast can be described, but the non-inferiority decision cannot be independently assessed from the available information.
The arm-level estimates are both negative, indicating that the estimated mean A1C change from baseline was downward in each group. This describes the posted estimates, not a conclusion about treatment efficacy. The interval estimates around each arm mean also show that those values are estimates rather than exact measurements of a group-wide effect. The group contrast is the more direct statistic for comparing the randomized treatments.
Secondary endpoint results address related but distinct questions, including fasting plasma glucose and achievement of specified A1C goals. Their overall pattern does not overturn the interpretive limitation of the primary endpoint: a non-inferiority margin is needed to assess the stated primary claim. The secondary comparisons are also not substitutes for the primary analysis, particularly because adjustment for multiple testing is not reported in the registry record.
Sample-size illustrations based on observed secondary effects are planning exercises, not evidence about the trial’s observed power. General power calculations describe how a hypothetical future design might perform under stated assumptions; they cannot repair missing protocol details or establish the probability that a result is true. Those illustrations should therefore be read as design aids, not as confirmation of a clinical or statistical conclusion.
9. Statistical Methods Explained
The primary endpoint is continuous, and the registry reports least squares mean change from baseline for each arm. A least squares mean is generally a model-based estimate of an average, often adjusted for variables included in a statistical model. The registry record does not report the model specification, the covariates, or the handling of repeated measurements. The posted estimates can be interpreted as least squares means, but the exact adjustment process cannot be reconstructed from the record.
What does the confidence interval convey?
In general, a confidence interval expresses statistical uncertainty around an estimate under the method used to calculate it. A narrower interval indicates greater precision than a wider interval, all else being equal. It does not describe the spread of individual participant measurements, and it does not show that every value inside the interval is equally likely. For the primary contrast, the registry reports a 95% confidence interval from -0.15 to 0.08 around the difference in least squares means. Because it spans zero, the interval includes no difference as one value compatible with the reported estimate and method.
A confidence interval should be interpreted in relation to the scientific question. For a conventional superiority question, an interval spanning zero is often discussed as not distinguishing the contrast from no difference at the stated confidence level. For non-inferiority, the key reference is instead the margin defining an unacceptable loss. The margin is not reported in the registry record, so the interval cannot be assessed against that threshold. The registry also does not report a primary p-value or a complete primary decision rule.
Why does the non-inferiority margin matter?
In general, non-inferiority tests whether the evidence rules out a disadvantage greater than a prespecified margin. The margin must be defined before interpreting the results; it is not chosen by looking at the observed estimate. A point estimate close to zero is not sufficient, because the uncertainty interval may still include values beyond an acceptable margin. Without the margin and analysis rules, the posted primary result cannot be translated into a verified non-inferiority conclusion.
What is the role of the secondary comparisons?
The secondary outcomes include binary thresholds for achieving an A1C goal, alongside a fasting plasma glucose outcome listed in the record. For binary outcomes, an analysis may compare event proportions or their difference. The registry reports sponsor analyses of between-group rate differences for the posted A1C-goal outcomes, using the Miettinen & Nurminen method. That method is identified for those sponsor comparisons; the method for the primary continuous endpoint is not reported in the registry record.
Additional unadjusted calculations use the posted event counts and group sizes to estimate risk differences, confidence intervals, and p-values. These are simple, unadjusted recalculations from summary statistics, not replacements for the sponsor’s analysis. Differences between recalculated and sponsor-reported values can arise because the sponsor used a specified method and because the posted percentages and counts may be rounded. The registry does not flag a discrepancy. Unadjusted p-values do not account for the fact that multiple secondary questions are examined, so they should be treated as exploratory unless a multiplicity plan says otherwise. Such a plan is not reported in the registry record.
How should over-dispersion be understood?
Over-dispersion is a general issue for count or binary-data models when observed variability exceeds what a model assumes. It can make model-based standard errors too small if not handled appropriately. The registry’s posted A1C-goal analyses identify a method for the between-group rate difference, but the record does not describe an over-dispersion assessment or a related modeling approach. There is no basis to claim that over-dispersion affected these analyses; the concept is relevant only as a general consideration in statistical modeling.
What do the planning calculations mean?
The sample-size illustrations use observed effects and state assumptions including a two-sided significance level of 0.05, equal allocation, and a normal approximation. They show hypothetical participants per arm for specified power targets and effect fractions. These are planning illustrations, not observed power, and not evidence that the original trial was designed using those assumptions. The trial’s own sample-size justification and planning assumptions are not reported in the registry record.
Power is a design property calculated under assumptions about an effect, variability, significance level, and analysis. It is not a retrospective probability that a result is correct. Planning calculations based on observed effects can be especially sensitive to the size of the observed effect, so their proper use is to illustrate possible future design requirements under the stated assumptions—not to validate the result or to infer the trial’s original design.
10. Analyses Reported by the Sponsor
| Method | Estimate | 95% CI | P-value |
|---|---|---|---|
| not stated | Difference in least squares mean -0.03 | -0.15 to 0.08 | not reported |
The registry reports the sponsor’s primary comparison as a difference in least squares means of -0.03, with a 95% confidence interval from -0.15 to 0.08. The record does not provide a p-value for this primary comparison. The sponsor analysis is the only posted inferential analysis for the primary continuous endpoint. A separate recalculated two-arm estimate is not available for that endpoint, so there is no direct recalculation against which to check the sponsor’s primary result. The registry does not flag a discrepancy.
For the posted A1C-goal outcomes, the sponsor reports between-group rate differences using the Miettinen & Nurminen method. The simple unadjusted recalculations from the posted summary counts produce estimates and p-values that are not identical to those sponsor-reported analyses. These calculations answer a related comparison using a different, explicitly unadjusted route; they should not be treated as corrections to the sponsor’s analysis. The sponsor method and its reported results take precedence for describing the registry’s own analysis.
Agreement or difference between methods does not by itself establish the validity of either approach. The available information does not include every detail needed to reproduce the sponsor analyses, such as all model specifications or analysis conventions. The sponsor results should therefore be reported as posted, while recalculations should be clearly identified as supplementary unadjusted checks rather than as the trial’s prespecified analysis.
11. Multiplicity, Missing Data and Analysis Populations
Multiplicity arises when a study evaluates more than one outcome, comparison, or analysis. In general, repeated testing can increase the chance of at least one apparently positive result even when no true effect exists. Prespecified approaches may control that risk through an ordered testing sequence, adjustment of significance thresholds, or another planned strategy. The registry record lists multiple secondary outcomes, but a multiplicity strategy, testing hierarchy, or adjustment is not reported in the registry record. The posted secondary p-values should therefore be read as unadjusted evidence, not as family-wise controlled confirmatory tests.
The record identifies the primary endpoint population as randomized participants who received at least one dose of study treatment and had a baseline measurement or a post-randomization measurement for the endpoint after at least one dose. This definition is narrower than a population consisting of every randomized participant, because it requires treatment exposure and an eligible endpoint measurement. The registry does not report the number excluded from this analysis population or the reasons for any exclusions.
Missing-data handling is not reported in the registry record. The record does not explain whether missing Week 24 outcomes were imputed, modeled under a repeated-measures approach, handled through another method, or left out of the analysis. It also does not provide sensitivity analyses assessing how different assumptions about missing outcomes might affect the primary estimate. These details matter because the validity and interpretation of an estimate can depend on the amount, pattern, and assumed mechanism of missingness.
The registry record does not report interim analyses, stopping rules, or a detailed statistical analysis plan. It also does not provide the primary non-inferiority margin or the full decision rule. These are not minor omissions for interpreting a non-inferiority study: without the margin, analysis population details, and missing-data methods, the posted estimate is informative as a reported contrast but cannot be independently evaluated against all relevant design safeguards.
12. Safety Results
The registry reports serious adverse events as affected participants divided by participants at risk.
| Arm | Participants with serious adverse events | Participants at risk | Percentage |
|---|---|---|---|
| Omarigliptin 25 mg Once Weekly | 11 | 322 | 3.4% |
| Sitagliptin 100 mg Once Daily | 9 | 320 | 2.8% |
Other (non-serious) adverse events
Participants with at least one non-serious event at or above the registry's 5% reporting threshold.
| Arm | Participants affected of at risk |
|---|---|
| Omarigliptin 25 mg Once Weekly | 0 of 322 |
| Sitagliptin 100 mg Once Daily | 0 of 320 |
Most frequent serious adverse event terms
| Event term | Organ system | Omarigliptin 25 mg Once Weekly | Sitagliptin 100 mg Once Daily |
|---|---|---|---|
| Acute myocardial infarction | Cardiac disorders | 1 of 322 | 1 of 320 |
| Prostate cancer | Neoplasms benign, malignant and unspecified (incl cysts and polyps) | 2 of 322 | 0 of 320 |
| Angina pectoris | Cardiac disorders | 1 of 322 | 0 of 320 |
| Arrhythmia supraventricular | Cardiac disorders | 0 of 322 | 1 of 320 |
| Atrial fibrillation | Cardiac disorders | 0 of 322 | 1 of 320 |
| Myocardial infarction | Cardiac disorders | 0 of 322 | 1 of 320 |
| Myocardial ischaemia | Cardiac disorders | 1 of 322 | 0 of 320 |
| Vertigo | Ear and labyrinth disorders | 0 of 322 | 1 of 320 |
| Hypothyroidism | Endocrine disorders | 1 of 322 | 0 of 320 |
| Non-cardiac chest pain | General disorders | 0 of 322 | 1 of 320 |
Serious events with the highest arm-level rate: prostate cancer (0.6%), acute myocardial infarction (0.3%), arrhythmia supraventricular (0.3%), atrial fibrillation (0.3%), myocardial infarction (0.3%).
The registry lists serious adverse events affecting 11 participants in the omarigliptin group and 9 in the sitagliptin group. The stated numbers at risk are 322 in the first group and 320 in the second. These are counts recorded for the groups, not estimates of a causal treatment effect. A difference in counts alone does not establish that one treatment caused more serious events; interpretation would require event definitions, follow-up and exposure context, and an appropriate comparative analysis.
The record also lists several serious-event terms with percentages, including prostate cancer at 0.6% and acute myocardial infarction at 0.3%. The listed percentages are not enough to establish comparative risks between arms, and the registry entry does not give group-specific estimates for each term in the information presented. The other-event count is listed as 0 for each group. Death counts are not reported in the registry record.
Serious adverse-event summaries describe events recorded during the study, but they do not by themselves establish whether an event was caused by treatment. The available figures should be read as descriptive safety reporting, not as a complete comparison of all risks or as medical advice.
13. What the Result Does, and Does Not, Mean
The posted primary estimate describes a small difference between the least squares mean A1C changes, with uncertainty extending to values on either side of zero. It shows what the registry reports for the Week 24 comparison in the defined analysis population. It does not reveal the exact effect for every participant, and it does not establish that the two treatments have identical effects.
Because the stated objective was non-inferiority, a conclusion depends on the prespecified margin and analysis rules. The margin is not reported in the registry record. The result therefore cannot be declared non-inferior solely because the point estimate is close to zero or because the confidence interval includes zero. Nor does the interval by itself establish superiority or equivalence. Those are distinct statistical claims with different criteria.
The secondary results add context about threshold attainment, but they are multiple outcomes and the record does not describe multiplicity control. Unadjusted findings should not be elevated to confirmatory conclusions. Likewise, the serious adverse-event counts are descriptive and cannot identify treatment causation from counts alone.
General statistical interpretation distinguishes an estimate from a decision: estimates summarize the observed data under an analysis, while decisions require a prespecified framework and attention to uncertainty. Here, the posted values support a description of the observed group estimates and their precision. Missing details about the non-inferiority margin, analysis model, missing data, and multiplicity limit what can be concluded from the registry record alone. No treatment recommendation follows from these statistics.
14. Why This Trial Matters Statistically
This trial raises a central statistical issue in non-inferiority research: a near-zero estimated contrast is not, by itself, the criterion for non-inferiority. The confidence interval must be interpreted against a prespecified margin, and the analysis must follow a documented decision rule. Since the margin is not reported in the registry record, the central inferential threshold cannot be checked from the posted entry.
The design also illustrates the value of distinguishing the arm-level mean changes from the between-group contrast. Both arm estimates describe change from baseline, but the randomized comparison is captured by the difference between the arms and its uncertainty. Reporting the contrast alongside its interval makes the precision question visible; the interval indicates that the data do not pin down a single exact difference.
Secondary threshold outcomes can be useful complements to a continuous primary measure, but testing several outcomes creates interpretive challenges. Without a reported multiplicity plan, individual unadjusted p-values should be treated cautiously. Likewise, hypothetical sample-size calculations based on observed secondary effects are useful as planning illustrations only. They are not evidence of observed power and do not establish the original design’s adequacy.
Finally, registry results are most informative when design, analysis populations, missing-data procedures, and safety reporting can be interpreted together. This record supplies the principal endpoint estimates and some secondary and safety summaries, while leaving several analysis details unreported. That distinction helps keep the statistical reading focused on what the posted estimates show without extending them beyond the stated evidence.
15. 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 details needed for an independent assessment are not reported in the registry record. Most importantly, the non-inferiority margin and complete primary decision rule are absent, so the principal hypothesis cannot be evaluated against its stated threshold. The primary statistical model and its covariates are also not reported, limiting reproducibility of the least squares mean estimates.
The analysis population definition requires treatment exposure and an eligible endpoint measurement, but the record does not state how many randomized participants were omitted or why. Missing-data methods, sensitivity analyses, and handling of rescue therapy in the efficacy analysis are not reported in the registry record. The arm descriptions allow glimepiride as rescue therapy, but do not explain how its use was incorporated into outcome analyses.
The registry lists secondary outcomes but does not report a multiplicity procedure or testing hierarchy. One listed secondary outcome, fasting plasma glucose, has no result among the posted secondary results; its findings are not reported in the registry record. Details of allocation concealment, adherence, and laboratory procedures are also not available in the record’s stated details.
The serious-event information is limited to counts and selected terms. Death counts are not reported, and event-specific comparative estimates or causal assessments are not provided. These limitations do not erase the posted results, but they constrain independent evaluation of the design, analysis, and safety patterns.
16. Related Tutorials
17. Related Statistical Calculators
18. Sources
- ClinicalTrials.gov: Study to Evaluate the Safety and Efficacy of the Addition of Omarigliptin (MK-3102) Compared With the Addition of Sitagliptin in Participants With Type 2 Diabetes Mellitus With Inadequate Glycemic Control on Metformin (MK-3102-026) — NCT01841697.
- Registry record last updated 2018-09-10; status last verified 2018-08.
- Results first posted 2015-11-25.
- 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.
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19. Record Summary
The registry describes a completed phase III, multicenter, double-blind, randomized, parallel-group study of omarigliptin versus sitagliptin added to metformin in participants with type 2 diabetes and inadequate glycemic control. The primary endpoint was change from baseline in A1C at Week 24. The reported difference in least squares mean change was -0.03, with a 95% confidence interval from -0.15 to 0.08.
The stated primary hypothesis was non-inferiority, but the margin is not reported in the registry record. Secondary results include A1C-goal outcomes; their sponsor-reported comparisons and unadjusted recalculations should be interpreted cautiously because multiplicity control is not reported. Serious adverse-event counts are descriptive, and deaths are not reported in the registry record.
The available estimates describe the posted results and their uncertainty. Missing details about the non-inferiority criterion, analysis model, and handling of missing data limit independent assessment of the primary conclusion.