Efficacy and Safety of Semaglutide Once-weekly Versus Placebo as add-on to Basal Insulin Alone or Basal Insulin in Combination With Metformin in Subjects With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Semaglutide Once-weekly Versus Placebo as add-on to Basal Insulin Alone or Basal Insulin in Combination With Metformin in Subjects With Type 2 Diabetes (NCT02305381), a randomized phase 3 study. The primary outcome is Change in HbA1c (Glycosylated Haemoglobin).

2. Clinical Question

The endpoint is a continuous measure, so the central comparison is the difference between adjusted mean changes rather than a count of people who crossed a threshold. The registry reports separate comparisons for each semaglutide dose against placebo. It gives estimated mean changes for all three groups and sponsor-reported treatment differences with confidence intervals and p-values.

The trial record describes an international study conducted in Asia, Europe and the United States of America. Its primary question is about change in HbA1c at week 30 in the defined analysis population; it does not, by itself, establish how results might differ for people outside that population or under other treatment conditions.

3. Trial Design

This was a phase 3, randomized, double-masked, parallel-group trial sponsored by Novo Nordisk A/S. The registry reports an enrollment of 397 and a completed status. The recorded start date is 2014-12-01 and the primary completion date is 2015-11-21. The trial was conducted in Asia, Europe and the United States of America.

The groups received semaglutide 0.5 mg, semaglutide 1.0 mg or placebo. The stated purpose was to investigate semaglutide once weekly versus placebo as an addition to basal insulin alone or basal insulin combined with metformin in people with type 2 diabetes. The registry arms list two placebo groups, one corresponding to each semaglutide dose comparison. The arm descriptions do not provide further detail about the dosing schedule beyond the names and doses recorded.

Randomization is intended to reduce systematic differences between treatment groups at allocation, while masking is intended to limit the influence of treatment knowledge on care and assessment. A parallel-group design assigns participants to a group and compares outcomes between groups. These are general descriptions of the design features; the registry record does not report additional implementation details, such as the randomization sequence method or the specific masking procedures.

The primary endpoint was assessed from week 0 to week 30. The primary analysis population included randomized participants who had received at least 1 dose of randomized semaglutide or placebo. The registry also lists secondary outcomes, including body weight, fasting plasma glucose, insulin dose, blood pressure, treatment satisfaction and HbA1c threshold measures. Further details on the original sample-size justification and the trial’s planned multiplicity strategy are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set included all randomised subjects who had received at least 1 dose of randomised semaglutide or placebo.

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: Analysis was performed on full analysis set which included all randomised subjects who had received at least 1 dose of randomised semaglutide or placebo.

6. Primary Endpoint

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

The primary endpoint is estimated mean change in glycated haemoglobin, or HbA1c, from baseline (week 0) to week 30. HbA1c reflects glycosylated haemoglobin and is used in diabetes research as a continuous measure of glycaemic status over time. A change score expresses how the measure at follow-up differs from baseline. The registry reports the unit as percentage of glycosylated hemoglobin.

Using a continuous endpoint retains information about the amount of change across participants rather than reducing the result to whether each participant did or did not meet a cutoff. The registry also lists threshold outcomes as secondary measures, but the primary analysis is the estimated mean change at week 30. This makes the treatment contrast a comparison of average changes between each semaglutide group and placebo.

The posted estimates are least-squares means, not simple raw arithmetic averages. According to the registry description, the estimates are adjusted for baseline value and the model’s listed factors, with mean estimates adjusted according to the observed baseline distribution. This approach aims to compare groups while accounting for specified features of the design and baseline measurements.

HbA1c is used as an endpoint for comparing changes over the trial period. Its value as a study measure does not mean that this single result fully characterizes every outcome that matters to participants. The registry includes additional outcomes, and the posted primary endpoint concerns the specified week 30 comparison rather than all possible effects or longer-term outcomes.

7. Results Posted in the Registry

• Semaglutide 0.5 mg: mean -1.45 versus -0.09 on control; difference -1.36 (95% CI -1.61 to -1.11), standardized effect d = -1.31; z-test p = <0.001.
• Semaglutide 1.0 mg: mean -1.85 versus -0.09 on control; difference -1.76 (95% CI -2.01 to -1.51), standardized effect d = -1.70; z-test p = <0.001.

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 Body Weight

• 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:
  • Semaglutide 0.5 mg: mean -3.67 versus -1.36 on control; difference -2.31 (95% CI -3.32 to -1.30), standardized effect d = -0.55; z-test p = <0.001.
  • Semaglutide 1.0 mg: mean -6.42 versus -1.36 on control; difference -5.06 (95% CI -6.07 to -4.05), standardized effect d = -1.21; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Semaglutide 0.5 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Semaglutide 1.0 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Fasting Plasma Glucose (FPG)

• 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:
  • Semaglutide 0.5 mg: mean -29.14 versus -8.51 on control; difference -20.63 (95% CI -31.39 to -9.87), standardized effect d = -0.46; z-test p = <0.001.
  • Semaglutide 1.0 mg: mean -42.38 versus -8.51 on control; difference -33.87 (95% CI -44.66 to -23.08), standardized effect d = -0.76; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Semaglutide 0.5 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Semaglutide 1.0 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Insulin Dose

• 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:
  • Semaglutide 0.5 mg: mean 0.90 versus 0.96 on control; difference -0.06 (95% CI -0.09 to -0.03), standardized effect d = -0.52; z-test p = <0.001.
  • Semaglutide 1.0 mg: mean 0.85 versus 0.96 on control; difference -0.11 (95% CI -0.14 to -0.08), standardized effect d = -0.96; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Semaglutide 0.5 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Semaglutide 1.0 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary measures covering body weight, fasting plasma glucose, insulin dose, systolic and diastolic blood pressure, diabetes treatment satisfaction and HbA1c threshold outcomes. The detailed numerical summaries include body weight, fasting plasma glucose and insulin dose. For those measures, both semaglutide groups have negative estimated changes or treatment differences relative to placebo in the posted comparisons. Those directions are broadly consistent with the primary HbA1c result in the limited sense that the estimated group contrasts point away from placebo; they do not make the measures interchangeable or establish a single overall treatment effect.

Secondary outcomes can help describe other dimensions of the trial, but they answer distinct questions and may have different measurement scales, variability and interpretation. Their estimates should be read from the relevant tables rather than inferred from the primary endpoint. The registry lists seven posted secondary outcomes, but not every listed measure has detailed numerical results represented in the data. Where a result is not shown, its estimate is not reported in the registry record.

Unadjusted secondary p-values carry less weight when many outcomes or comparisons are examined because the chance of at least one apparently unusual result can rise as the number of tests increases. General statistical principle: multiplicity procedures can control that risk, but the registry record does not report a multiplicity adjustment for the secondary outcomes. The findings are therefore best treated as supporting descriptions rather than as a set of independent confirmatory claims. They also do not alter the primary endpoint’s definition or its model-based analysis.

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

• Change in Body Weight
• Change in Fasting Plasma Glucose (FPG)
• Change in Insulin Dose
• Change in Systolic and Diastolic Blood Pressure
• Patient Reported Outcomes, Diabetes Treatment Satisfaction Questionnaire (DTSQ)
• HbA1c Below 7.0% (53 mmol/Mol) American Diabetes Association (ADA) Target
• HbA1c Below or Equal to 6.5% (48 mmol/Mol) American Association of Clinical Endocrinologists (AACE) Target

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, and the registry reports least-squares mean changes with standard errors. A least-squares mean is a model-based estimate of a group mean after accounting for terms specified in the analysis. Here, the registry states that post-baseline responses were analyzed using a mixed model for repeated measurements. The treatment effects are reported as treatment differences between a semaglutide group and placebo.

What does a repeated-measures model do?

In general, a repeated-measures model analyzes a participant’s measurements across visits together rather than treating each visit as an unrelated observation. This can use the pattern of available follow-up measurements and account for the fact that measurements from the same participant are related. The registry identifies treatment, country and a stratification variable as fixed factors, with baseline value as a covariate; these terms are nested within visit. It also says estimates are adjusted according to the observed baseline distribution.

The stratification variable combined HbA1c level at screening with use of metformin. The record describes the HbA1c categories as at or below 8.0% or above 8.0%, crossed with metformin use as yes or no. Including specified design and baseline factors can adjust the comparison for those measured features. The registry does not report further model specifications such as the covariance structure, degrees-of-freedom method or sensitivity analyses; those details are not reported in the registry record.

How should the standard error be read?

A standard error describes the estimated uncertainty in a model-based mean, rather than the spread of individual participant values. Smaller standard errors generally indicate more precise estimates, all else equal. The posted group means have standard errors of 0.09. The confidence intervals for treatment differences provide a more direct view of uncertainty around the between-group contrasts. General statistical interpretation: a confidence interval is a range of values compatible with the data and the analysis procedure at its stated confidence level; it is not a range containing a fixed proportion of individual responses.

What do the p-values tell us?

A p-value summarizes how incompatible the observed data are with a specified null hypothesis under the test’s assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The sponsor reports p < 0.001 for both primary comparisons. The re-calculated unadjusted p-values are p < 0.001. They come from a simpler calculation based on the posted summary statistics and are not a replacement for the sponsor’s model-based analysis.

In general, adjustment for baseline values and design factors can make the model-based comparison differ from a simple comparison of group summaries. The registry’s reported analysis and the re-calculation are close, and the discrepancy indicator is false. The sponsor’s own analysis is therefore reported alongside, rather than displaced by, the simple re-calculation.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variation is greater than a statistical model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow; if it accounts for the variation appropriately, uncertainty is better represented. Over-dispersion is especially discussed for count or binary outcomes, whereas this primary endpoint is continuous. The registry does not identify an over-dispersion issue for this endpoint, and a particular over-dispersion adjustment is not reported in the registry record.

The record says missing post-baseline data were imputed using the mixed model for repeated measurements. In general, model-based handling of missing observations relies on assumptions about the relationship between observed and missing measurements. The registry does not describe the assumptions in detail, quantify missingness or report sensitivity analyses for departures from those assumptions. The analysis population is the full analysis set: randomized participants who received at least 1 dose of randomized semaglutide or placebo.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for the semaglutide 0.5 mg treatment difference is -1.61 to -1.10, around an estimate of -1.35. For semaglutide 1.0 mg, the reported interval is -2.01 to -1.50, around an estimate of -1.75. Both intervals lie below zero, which is consistent with the negative treatment-difference estimates in the posted analysis. The intervals give a range of plausible values for the treatment contrast under the model and its assumptions, not a guarantee that the true value lies inside them.

The re-calculated intervals are -1.609 to -1.111 for the 0.5 mg comparison and -2.009 to -1.511 for the 1.0 mg comparison. These are unadjusted calculations from posted summary statistics, while the sponsor’s intervals come from the mixed-model analysis. Their close alignment is useful as a check on the scale and direction of the posted result, but the model-based results remain the registry’s reported analysis.

Precision is about the uncertainty in an estimate, not whether an outcome is important. A narrower interval indicates less statistical uncertainty under the analysis assumptions; it does not show how much participants vary or resolve questions the endpoint did not measure. The interval endpoints are rounded in the registry, so small apparent differences between the displayed estimate and interval midpoint should not be treated as meaningful.

The registry gives a standard error of 0.09 for each group’s estimated mean change. That quantity reflects uncertainty in each estimated mean and should not be confused with a standard deviation describing participant-to-participant variation. The treatment-difference intervals are the more direct summary of precision for the primary comparison. The record does not report alternative confidence intervals under different missing-data assumptions or model specifications.

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 table and curve are planning illustrations based on the observed effects in the posted results, not on the original trial design. For the continuous outcomes shown, figures are participants per arm. The stated illustration uses a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified effect under those planning assumptions, if that effect is the true one. The 90% power column gives the corresponding number for a 90% chance. These are planning quantities, not descriptions of the actual analysis population. The 80% and 90% columns refer to different target probabilities of detecting the assumed effect, not to confidence levels or the probability that the result is true.

The table varies the assumed effect from 100% of the observed effect to 75% and 50%. Smaller effects require more participants to detect, all else equal, so the smaller-effect scenarios have larger planning requirements. For example, for the semaglutide 0.5 mg primary comparison, the illustration gives 10 participants per arm for 80% power at 100% of the observed effect, and 37 participants per arm at 50% of the observed effect. These figures are illustrations only; they do not establish what the trial originally planned or why it enrolled its reported number.

This is not observed power. For time-to-event outcomes, the stated convention would be total events, but the outcomes are continuous and the displayed figures are per arm.

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 = -1.360; pooled standard deviation σ = 1.036.
2. n = 2 × (1.96 + 0.842)² × 1.036² / -1.360² = 9.1, rounded up to 10 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 <- -1.36                      # observed difference in means
sigma <- 1.03598523118795                     # 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(2305381)
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 = 10 (80% power), 13 (90% power)
 75% of observed effect: n per arm = 17 (80% power), 22 (90% power)
 50% of observed effect: n per arm = 37 (80% power), 49 (90% power)
power.t.test: 10.2 
Simulated power at n = 10 per arm: 0.798 (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 registry’s sponsor-reported primary analysis uses a mixed model for repeated measurements and gives treatment differences of -1.35 for semaglutide 0.5 mg and -1.75 for semaglutide 1.0 mg versus placebo. The associated 95% confidence intervals are -1.61 to -1.10 and -2.01 to -1.50, respectively, with p < 0.001 for each comparison.

The re-calculated comparisons use posted group summaries and approximate standard deviations derived from the reported standard errors. They are unadjusted calculations and give differences of -1.36 and -1.76, with intervals of -1.609 to -1.111 and -2.009 to -1.511. The registry marks the discrepancy indicator as false. The estimates and intervals are closely aligned, while the methods differ: the sponsor’s model incorporates repeated measurements and the listed adjustment factors, whereas the recalculation does not reproduce that full analysis.

Accordingly, the sponsor’s analysis is the main basis for describing the primary result. The recalculation is a transparent cross-check using the posted summaries, not an alternative fitted model or a replacement for the registry analysis. Its p-values, reported as p < 0.001, should be kept distinct from the sponsor’s model-based p-values.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is described as the full analysis set, including all randomized participants who received at least 1 dose of randomized semaglutide or placebo. This definition differs from a population restricted to participants who completed every visit. The registry does not report the number excluded from this set or the completeness of follow-up by group.

The primary analysis uses a mixed model for repeated measurements, and the record says missing data were imputed using that model. In general, a repeated-measures model can use available post-baseline measurements without requiring a single completed value at every visit. Its interpretation still depends on assumptions about missing observations and the relationship between observed and unobserved data. The registry does not report the amount or pattern of missingness, detailed imputation assumptions, or sensitivity analyses addressing alternative assumptions.

Multiplicity concerns arise when several hypotheses are tested, including multiple doses, secondary outcomes and possibly multiple time points. The registry reports two primary dose-versus-placebo comparisons and lists multiple secondary outcomes. A prespecified strategy for controlling multiplicity, or a statement that no adjustment was planned, is not reported in the registry record. The p-values for the primary comparisons should therefore be understood as reported for those comparisons, without assuming an unreported adjustment. Secondary results without a reported multiplicity procedure warrant particular caution.

The model description identifies treatment, country and the combined stratification variable as fixed factors, baseline value as a covariate, and the factors as nested within visit. Other technical details, including the covariance structure, are not reported in the registry record. The original sample-size justification, interim-analysis plans and any broader statistical analysis plan are also not reported in the registry record. Their absence from the record means the analysis cannot be assessed against those unreported details.

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: back pain (0.8%), carotid artery stenosis (0.8%), carotid endarterectomy (0.8%), cholecystitis acute (0.8%), clostridium difficile colitis (0.8%).

The registry reports serious adverse events for 8 of 132 participants in the semaglutide 0.5 mg group, 12 of 131 in the semaglutide 1.0 mg group and 9 of 133 in the placebo group. These are counts of participants affected among those at risk in each group. They are not event rates per unit of follow-up, and they do not by themselves establish whether an event was caused by treatment.

The listed serious-event terms each have a reported frequency of 0.8%: back pain, carotid artery stenosis, carotid endarterectomy, acute cholecystitis, Clostridium difficile colitis and coronary artery bypass. These terms describe the events identified in the registry’s listing; the record does not provide enough detail to compare their timing, duration or clinical course. Death counts are not reported in the registry record.

Safety comparisons require attention to the number of participants observed, follow-up duration, definitions and ascertainment. Those details are not fully specified in the figures. The counts should therefore be read descriptively, not as proof of equal or different risks between groups.

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

The primary result describes estimated average HbA1c change from baseline to week 30 in the defined analysis population. The model-based treatment differences are negative for both semaglutide doses relative to placebo, and both reported 95% confidence intervals are below zero. The posted estimates therefore show a difference in adjusted mean change between each semaglutide group and placebo under the analysis described in the registry.

This finding is not the same as saying that every participant experienced the group average, or that every person’s outcome changed in the same direction. A mean summarizes a group; it does not describe the full distribution of individual responses. Nor does a small p-value quantify the size or practical importance of a difference. The registry provides a statistical comparison, but it does not establish a threshold for what should be considered clinically important.

The result is specific to the study population, the treatment regimens, the comparator, the endpoint and the week 30 assessment. It does not show what happened beyond the reported time point, nor does it settle the interpretation of every secondary outcome. The record also does not provide the missing-data sensitivity analyses or multiplicity strategy needed to assess those aspects fully.

Safety counts are also descriptive and cannot establish causation from the information presented. The trial’s outcome estimates should be considered alongside the study design and limits of the registry record. This page reports statistical results; it is not a recommendation about treatment or a substitute for clinical judgment.

18. Why This Trial Matters Statistically

This trial is statistically useful because it reports a continuous primary endpoint alongside a model-based comparison of two dose groups with placebo. The design features recorded in the registry—randomization, masking and parallel groups—support a structured between-group comparison, while the repeated-measures model uses the trial’s longitudinal outcome framework and adjusts for specified baseline and design factors.

The result also illustrates why an estimate, its interval and the analysis method should be read together. The treatment differences are accompanied by confidence intervals and p-values, and simple calculations from the posted summaries provide a separate check on direction and approximate scale. The recalculation is close to the sponsor result but does not reproduce the sponsor’s model. Keeping those methods distinct prevents a summary-statistic calculation from being mistaken for the primary analysis.

The registry record also shows what cannot be concluded from statistical significance alone. The primary endpoint is one measure at one time point; secondary outcomes cover other dimensions, and their interpretation depends partly on multiplicity. Missing-data handling is described at a high level, but important details are absent. Sample-size illustrations based on observed effects can support planning discussions, but they cannot explain the original design in the absence of a reported justification.

For biostatistical readers, the key lesson is to connect the target estimand, analysis population, model, uncertainty and reporting gaps. The numerical result is informative within those boundaries; sound interpretation depends on keeping the boundaries visible.

19. Limitations

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

The registry record describes the primary repeated-measures model but omits technical details needed for a full independent reconstruction, including the covariance structure and other fitting choices. It says missing data were imputed using the model, but does not quantify missingness, describe its pattern or report sensitivity analyses under alternative missing-data assumptions.

The full analysis set is defined as randomized participants who received at least 1 dose, but the record does not give a detailed participant flow in the information. The original sample-size calculation and its assumptions are not reported in the registry record, so the enrollment figure cannot be evaluated against the trial’s intended power or design effect. The planning figures on this page are illustrations based on observed effects, not evidence of the original design rationale.

The record reports two primary dose comparisons and multiple secondary outcomes, but a multiplicity strategy is not reported. This limits how confidently the family of statistical claims can be interpreted, particularly for secondary findings. Detailed results are not available for every listed secondary measure, and absent results should not be inferred from the outcomes that do have estimates.

Safety summaries provide counts of participants with serious events and a short list of event terms. The information does not establish event timing, duration, exposure-adjusted rates or causal attribution. Death counts are not reported in the registry record. Finally, the primary endpoint concerns week 30; longer-term outcomes are not described by this endpoint result.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Semaglutide Once-weekly Versus Placebo as add-on to Basal Insulin Alone or Basal Insulin in Combination With Metformin in Subjects With Type 2 Diabetes — NCT02305381.
• Registry record last updated 2019-06-11; status last verified 2019-05.
• Results first posted 2018-02-19.
• 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

This completed, randomized, double-masked, phase 3 parallel-group trial compared once-weekly semaglutide 0.5 mg and 1.0 mg with placebo as an addition to basal insulin, with or without metformin, in people with type 2 diabetes. The registry reports enrollment of 397 and an international study conducted in Asia, Europe and the United States of America.

The primary endpoint was estimated mean HbA1c change from week 0 to week 30 in the full analysis set. The sponsor’s mixed-model analysis reported treatment differences of -1.35 and -1.75 for the two semaglutide doses versus placebo, with 95% confidence intervals below zero and p < 0.001 for both comparisons. The registry also lists secondary outcomes and serious adverse-event counts.

Interpretation is bounded by unreported details on the original sample-size rationale, multiplicity, missingness and some model specifications. The estimates describe the posted analysis at the specified time point and should be read with those limitations in view.