Efficacy and Safety of Semaglutide Once-weekly Versus Sitagliptin Once-daily as add-on to Metformin in Subjects With Type 2 Diabetes (SUSTAIN - CHINA MRCT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Semaglutide Once-weekly Versus Sitagliptin Once-daily as add-on to Metformin in Subjects With Type 2 Diabetes (SUSTAIN - CHINA MRCT) (NCT03061214), a randomized phase 3 study. The primary outcome is Change in HbA1c.

2. Clinical Question

The clinical question is comparative rather than a comparison with no treatment: both groups received an active glucose-lowering medicine alongside metformin. There are two semaglutide dose groups and one sitagliptin group, so the trial potentially addresses more than one contrast. Its stated aim was to compare the effects of the two once-weekly semaglutide dose levels with sitagliptin on glycaemic control after 30 weeks.

The record identifies a multinational trial conducted in Africa, Asia, Europe and South America. It does not report enough participant characteristics in the available record to define the population more precisely by age, disease duration, baseline HbA1c or other clinical features. Nor does it report the exact criteria used to determine whether a participant could enter the trial. Those details matter when judging how closely a trial population resembles a particular clinical setting, but they cannot be inferred from the treatment question alone.

The endpoint concerns an average change in a laboratory measure, not a direct count of complications, symptoms or other clinical events. The posted information therefore supports framing the study's question, but not answering whether either regimen produced a larger change or how precise a difference between regimens was. Numerical outcome comparisons and their uncertainty are not reported in the registry record in a form that reduces the endpoint to one comparison.

3. Trial Design

This was a phase 3, randomized, double-blind, double-dummy, active-controlled, parallel-group trial. The registry lists enrollment of 868 participants. The official title describes a 30-week trial; the primary endpoint is specified as change from week 0 to week 30. The study is described as multicentre and multinational, and the brief summary identifies Africa, Asia, Europe and South America as trial regions.

Participants were assigned to one of four regimens: semaglutide 0.5 mg once weekly with sitagliptin placebo once daily; semaglutide 1.0 mg once weekly with sitagliptin placebo once daily; sitagliptin once daily with semaglutide placebo 0.5 mg once weekly; or sitagliptin once daily with semaglutide placebo 1.0 mg once weekly. The active sitagliptin dose stated in the trial summary is 100 mg once daily. All participants were to remain on their stable pre-trial metformin.

Double-dummy masking means that matching placebos can be used to make regimens with different dosing schedules appear similar to participants and trial personnel. In this design, that is relevant because the active treatments differ in frequency: semaglutide was given once weekly and sitagliptin once daily. The record identifies double masking but does not specify which roles were masked or describe the procedures used to maintain masking.

Random allocation supports a comparison in which treatment assignment is not chosen by the participant or investigator. A parallel-group design means participants were assigned to a regimen and followed in that group, rather than crossing over between the active treatments. The record does not report the randomization sequence method, allocation-concealment procedures, stratification factors or the ratio of allocation to the four regimens. These implementation details should not be guessed from the design labels.

The record lists a start date of 2017-08-28, a primary completion date of 2019-03-14 and a completed status. Those dates describe the trial record, not the duration of treatment for an individual participant. The stated outcome assessment period for the primary endpoint is week 0 to week 30. Details of other visits, follow-up after treatment, adherence, discontinuation patterns and rescue treatment use are not reported in the registry record beyond the endpoint observation-period definitions.

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: Full analysis set comprised of all randomised participants."Number Analyzed" = participants with available data.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Full analysis set comprised of all randomised participants.

6. Primary Endpoint

The registry lists the primary outcome as Change in HbA1c, measured over Week 0, week 30.

The primary endpoint is change in HbA1c from baseline at week 0 to week 30. HbA1c is a measure of glycosylated haemoglobin used to assess glycaemic control over time. A change score expresses how the measure at the end of the assessment period differs from its baseline value; the registry specifies that the endpoint is summarized as a mean with standard deviation and uses percentage of glycosylated haemoglobin as its unit.

Mean change is useful for comparing the average response across randomized groups. It compresses each participant's baseline and follow-up measurements into a quantity that can be summarized at group level. It does not by itself describe the range of individual responses. The standard deviation describes variation among observations; it is not the same as the uncertainty around the group mean or around a between-group contrast. Confidence intervals, if reported, would address uncertainty in an estimate, but a numerical interval for the primary comparison is not reported in the registry record.

The registry distinguishes two observation periods. The on-treatment-without-rescue-medication period begins at the first dose and ends at either the last dose plus 7 days or the first initiation of rescue medication, whichever comes first. The in-trial period begins at randomization and continues to the final scheduled visit, including time after rescue medication begins or treatment is stopped early. These definitions target different summaries: one limits observations to a specified period while participants are treated without rescue medication, and the other retains follow-up through the scheduled final visit.

HbA1c is a surrogate measure of glycaemic control, not a direct measure of every health outcome relevant to participants. The registry also lists secondary outcomes involving body weight, glucose measurements and fasting hormones, but those do not replace the stated primary endpoint. The numerical primary results needed to judge the size and precision of the treatment contrast are not reported in the registry record in a single comparison.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

The registry describes a randomized parallel-group comparison. In general, randomization is intended to make treatment groups comparable at the point of assignment, including with respect to characteristics that are measured and those that are not. It does not guarantee identical groups in every trial, and it does not remove the need to report how assignment was generated and concealed. The registry record identifies randomized allocation but does not report the sequence-generation or allocation-concealment methods.

What does double-blind and double-dummy mean?

Masking is intended to reduce the influence of treatment knowledge on participant experience, care decisions, outcome assessment or reporting. A double-dummy approach is useful when active regimens have visibly different schedules: participants can receive matching active and placebo preparations so the treatment assignments are less apparent. The record says the trial was double-blind and double-dummy, but does not specify who remained masked, how emergency unmasking was handled or whether masking success was assessed. Those features should not be assumed.

What does a mean change summarize?

For a continuous outcome such as HbA1c, a mean change summarizes the average difference between follow-up and baseline measurements in a group. A between-group estimate compares those average changes across assigned regimens. The mean is informative about the center of the distribution, while the standard deviation describes spread among observations. Neither should be mistaken for the other. The standard deviation does not directly quantify the precision of a treatment contrast; precision is usually conveyed by a confidence interval or another uncertainty measure. The registry lists mean and standard deviation for the primary endpoint but does not provide a single comparative estimate or uncertainty interval in the record information summarized for interpretation.

In general, a confidence interval gives a range of estimates compatible with the data under the statistical model and procedure used. Its width reflects precision: a narrower interval indicates less uncertainty in the estimate, while a wider interval indicates more. An interval also helps distinguish a small, precisely estimated contrast from a larger but imprecise one. No confidence interval for the primary comparison is reported in the registry record here, so the endpoint description cannot establish precision.

Why are there different observation periods?

The registry defines an on-treatment-without-rescue-medication observation period and an in-trial observation period. The first is bounded by the first dose and either the last dose plus 7 days or the first rescue medication, whichever comes first. The second starts at randomization and extends to the final scheduled visit, including time after rescue medication or premature treatment discontinuation. These approaches answer related but distinct questions. Excluding observations after rescue medication or stopping treatment can describe outcomes during a specified treatment period, but it may omit later outcomes. Retaining follow-up through the scheduled visit describes the in-trial course, including events after changes in treatment. Neither definition alone tells the reader how missing measurements were handled or what statistical model was used.

What is over-dispersion, and why can it matter?

As a general statistical concept, over-dispersion occurs when observed variability is greater than a model assumes. It is most relevant to models for count data or other outcomes whose variability is constrained by their mean. If it is ignored, standard errors can be too small and uncertainty can appear understated. The primary endpoint is a continuous measure summarized by a mean and standard deviation, and the registry information does not identify a particular model or report an over-dispersion assessment. This general concept should not be mistaken for a description of the trial's analysis.

How should planning calculations be read?

The registry's sample-size assumptions describe a planning illustration based on an observed effect, with a two-sided significance level of 0.05, equal allocation between two arms and a normal approximation. The effect to detect is expressed as a stated fraction of the observed effect. These are illustrative assumptions rather than evidence about the original trial design. A planning sample size asks how many participants per arm might be required under specified assumptions; it does not measure the probability that the completed trial's finding is true. In particular, it is not observed power. The actual numerical planning results, the effect values used in those illustrations and the trial's own sample-size justification are not reported in the registry record.

In general, power depends on assumptions including the target effect, variability, significance level, allocation and analysis method. Changing those assumptions changes the planning result. A calculation based on an observed effect is especially dependent on that effect estimate, which may itself be imprecise. Such a calculation should be read as a planning illustration, not as a post-trial verdict about whether a study was adequate. For this trial, the stated illustration assumptions do not reveal the original protocol rationale, which is not reported in the registry record.

The record lists multiple outcome measures and analyses, but does not report the statistical model, covariate adjustment, missing-data assumptions, treatment of intercurrent events, or multiplicity procedure. These omissions limit how specifically the analysis can be reconstructed. General explanations of common statistical methods cannot fill those trial-specific gaps.

10. Multiplicity, Missing Data and Analysis Populations

The registry lists 74 outcome measures and 4 analyses. The primary endpoint is described across multiple categories or time points, and the record does not reduce it to one comparison. With more than one outcome, time point or treatment contrast, there can be more than one opportunity to observe a result that appears notable. In general, multiplicity procedures address the increased chance of misleading conclusions when several statistical tests are interpreted together. The registry record does not report whether such a procedure was planned or used, which comparisons were included in any family of tests, or how the primary comparisons were prioritized.

The record defines a full analysis set as all randomized participants and says that the number analyzed for an outcome is the number with available data. This identifies a population label and a count convention, but it does not explain how missing measurements were addressed. The missing-data mechanism, imputation method, sensitivity analyses and reasons for unavailable data are not reported in the registry record. Available-case analysis, imputation and other approaches make different assumptions; the stated number analyzed does not identify which approach was used.

The two endpoint observation periods also affect interpretation. The in-trial period includes follow-up after rescue medication or premature treatment discontinuation, while the on-treatment-without-rescue-medication period ends according to the specified treatment and rescue rules. The registry record does not provide a full statistical analysis plan explaining how observations after these events were used in estimation or how treatment discontinuation and rescue medication were handled analytically.

Other details that would help reproduce the analysis—including the model, covariates, variance assumptions and rules for outliers or protocol deviations—are not reported in the registry record. These are not minor technicalities: analysis choices can affect both the estimate and its uncertainty. Consequently, the available information supports identifying the target measure and analysis population definition, but not a complete account of the inferential procedure.

11. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastroenteritis (0.7%), road traffic accident (0.7%), abortion (0.3%), anal abscess (0.3%), arteriosclerosis coronary artery (0.3%).

The registry lists serious adverse event counts, other adverse event counts and deaths by treatment group. For semaglutide 0.5 mg, 287 participants were at risk for serious adverse events and 18 were affected; 287 were at risk for other adverse events and 135 were affected; deaths numbered 1. For semaglutide 1.0 mg, the corresponding counts were 290 at risk and 19 affected for serious adverse events, 290 at risk and 139 affected for other adverse events, and 1 death. For sitagliptin, the counts were 290 at risk and 12 affected for serious adverse events, 290 at risk and 89 affected for other adverse events, and 0 deaths.

The registry also lists serious adverse event terms and percentages: Gastroenteritis, 0.7%; Road traffic accident, 0.7%; Abortion, 0.3%; Anal abscess, 0.3%; Arteriosclerosis coronary artery, 0.3%; and Biliary colic, 0.3%. These terms are presented as serious adverse events, but the available information does not establish whether any event was judged related to treatment. The registry record does not provide a detailed event-by-event account or additional context for these terms.

At-risk and affected counts are descriptive. They do not alone show whether treatment caused an event or establish a comparative safety effect. Interpretation also depends on event definitions, observation time, exposure and how repeated events were counted; those details are not reported in the registry record. Death counts are reported as counts, without a cause-specific account in the available information. A numerical comparison should not be inferred from these descriptive figures alone.

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

The trial record describes a randomized comparison of two semaglutide doses with sitagliptin, each used alongside stable metformin. It identifies HbA1c change from week 0 to week 30 as the primary endpoint and defines two observation periods. It also lists secondary measures and descriptive safety counts. These features explain what the study was designed to examine, but the endpoint definition is not itself evidence about the comparative result.

The numerical primary comparison, its uncertainty and a p-value are not reported in the registry record in a single form that resolves the endpoint's several categories or time points. As a result, the size and direction of any between-group difference cannot be stated from the information available. Nor can statistical precision or the compatibility of the estimate with different possible effects be judged. This limitation is about the record content, not evidence that the trial found no difference.

Even when a numerical difference is reported, statistical evidence and clinical importance are distinct questions. Statistical uncertainty concerns how precisely the data estimate a contrast under an analysis; clinical importance concerns whether that contrast matters in the relevant setting. Judging clinical importance usually requires context such as meaningful-effect thresholds and the broader outcomes of interest. Such a threshold is not reported in the registry record, and it would not be appropriate to invent one.

The safety counts are likewise descriptive rather than proof of causation. Serious and other adverse event counts, as well as deaths, should be read with their group-specific at-risk counts and with caution about the absence of fuller information on exposure, event attribution and follow-up. The listed serious-event terms and percentages do not by themselves establish a treatment-related pattern.

The record does not provide the full statistical analysis plan, detailed handling of missing measurements, multiplicity procedures or the trial's sample-size justification. The planning illustration is explicitly not the original design calculation and should not be read as observed power. A defensible reading therefore separates what is documented—the design, endpoint definitions, population label and safety counts—from what remains unknown, including the numerical efficacy contrast and several analysis details. Nothing in this description is a recommendation about treatment choice.

13. Why This Trial Matters Statistically

This trial is statistically informative as an example of a multi-arm active-controlled design. It compared two doses of once-weekly semaglutide with once-daily sitagliptin, while all groups remained on stable metformin. The double-dummy approach addresses a practical masking challenge when regimens have different schedules. These design features help frame a fair comparison, while the registry's limited reporting of implementation details leaves some aspects of how the comparison was conducted unclear.

The primary endpoint is a continuous change measure, summarized as a mean and standard deviation. This makes clear why group-level estimates and uncertainty intervals are central to interpretation. A mean change alone would not convey how participants' responses varied, and a standard deviation is not the uncertainty around the between-group estimate. The registry description identifies the type of summary but does not provide a single numerical primary contrast in the information available for interpretation.

The two observation-period definitions also illustrate a recurring analytical issue. Results restricted to time on treatment without rescue medication and results retained through the in-trial period address different estimands, or treatment questions. Events such as rescue medication use and early discontinuation can affect which measurements contribute to each summary. Clear reporting of the chosen estimand, analysis method and missing-data assumptions is important for readers to understand what a reported treatment contrast represents. Those analysis details are not reported in the registry record.

With 74 outcome measures and 4 analyses, the distinction between a prespecified primary question and other analyses is important. Multiplicity procedures can influence how evidence from multiple comparisons should be interpreted, yet the record does not describe such procedures. The registry also describes a sample-size illustration based on an observed effect, but explicitly separates it from the trial's own design. This is a useful reminder that retrospective planning calculations are not observed power and do not establish why a trial enrolled its chosen number of participants.

The posted safety figures show counts by group, but descriptive counts are not a substitute for comparative estimation or causal assessment. Overall, the trial illustrates how design labels, endpoint definitions, analysis populations, uncertainty and reporting completeness all contribute to statistical interpretation. Its registry entry offers substantial design context but does not provide enough numerical primary-outcome information to assess the comparative effect.

14. 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.

A central limitation is that the primary endpoint is not presented as one numerical comparison. The registry explicitly notes several categories or time points, and the available information does not provide an estimate of the difference in HbA1c change between each semaglutide dose and sitagliptin, an uncertainty interval or a p-value. The record therefore does not support a conclusion about the magnitude, direction or precision of the primary treatment contrasts.

The record identifies the full analysis set as all randomized participants and defines the number analyzed as those with available data, but does not describe missing-data methods. It does not report the model used, adjustment variables, sensitivity analyses or how observations after treatment discontinuation and rescue medication were handled analytically. Because the endpoint is defined using two observation periods, the absence of a complete analysis description limits the ability to determine exactly what effect each analysis estimates.

The trial lists 74 outcome measures and 4 analyses but does not report a multiplicity strategy. It is therefore unclear how the different outcomes, time points and dose-specific comparisons were accounted for when interpreting statistical evidence. The record also does not provide the full randomization and allocation-concealment methods, the roles covered by masking, or the original sample-size justification. The planning illustration should not be mistaken for that justification.

Safety information is limited to group counts and a list of serious adverse event terms with percentages. Detailed event timing, attribution, recurrence, exposure duration and causes of death are not reported in the information available. These omissions prevent a more complete comparison of safety profiles and do not permit causal conclusions about individual events.

Participant characteristics beyond the type 2 diabetes population and stable metformin context are not included in the information available for this analysis. Without details such as baseline outcome values or other clinical characteristics, the applicability of the results to more specific populations cannot be evaluated. These limitations reflect what is not reported in the registry record; they should not be treated as evidence that a particular analysis or procedure was not performed.

15. Related Tutorials

16. Related Statistical Calculators

17. Sources

• ClinicalTrials.gov: Efficacy and Safety of Semaglutide Once-weekly Versus Sitagliptin Once-daily as add-on to Metformin in Subjects With Type 2 Diabetes (SUSTAIN - CHINA MRCT) — NCT03061214.
• Registry record last updated 2021-03-02; status last verified 2021-02.
• Results first posted 2020-04-09.
• 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.

18. Record Summary

NCT03061214 is a completed phase 3 randomized, double-blind, double-dummy, active-controlled, parallel-group trial with enrollment of 868. It compared semaglutide 0.5 mg or 1.0 mg once weekly with sitagliptin 100 mg once daily as add-on treatment to stable metformin. The official title describes a 30-week study, and the primary endpoint is change in HbA1c from week 0 to week 30.

The registry defines an on-treatment-without-rescue-medication period and an in-trial period, and identifies the full analysis set as all randomized participants. It lists 74 outcome measures and 4 analyses, along with group-level adverse event counts and selected serious adverse event terms. The numerical primary comparison is not reduced to one result because the outcome has several categories or time points. Statistical analysis details, missing-data procedures, multiplicity handling and the trial's own sample-size justification are not reported in the registry record available for interpretation.