Empagliflozin Add on to Linagliptin Study in Japanese Patient With Type 2 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Empagliflozin Add on to Linagliptin Study in Japanese Patient With Type 2 Diabetes Mellitus (NCT02453555), a randomized phase 3 study. The primary outcome is Change of Glycosylated Haemoglobin A1c (Glycosylated Haemoglobin A1c After 24 Weeks of Double-blind Treatment From Baseline).

2. Clinical Question

3. Trial Design

This was a Phase III, randomized, double-blind, parallel-group study, with a planned treatment period described as 52 weeks in the official title. The registry record reports enrollment of 275 and lists the study status as completed. The study start date was 2015-05-14, and primary completion was 2016-08-26. Boehringer Ingelheim is listed as the sponsor.

The primary outcome was assessed at Week 24, even though the official title describes a 52-week study. The listed primary analysis population was the full analysis set using observed cases, with participants analyzed according to randomized treatment assignment. The main arms for this endpoint were empagliflozin 10 mg/linagliptin 5 mg and linagliptin 5 mg plus placebo 10 mg. The registry also lists empagliflozin 25 mg/linagliptin 5 mg and placebo components among the interventions, and several secondary comparisons at Week 52.

Randomization assigns participants to study groups, while double masking is intended to keep treatment assignment unknown to participants and relevant study personnel. A parallel-group design compares groups receiving their assigned regimens over the study period rather than having each participant receive both regimens in sequence. These are general descriptions of the design terms; the registry does not report further operational details such as the randomization procedure or masking safeguards.

The registry record does not report the original sample-size justification, the trial’s detailed statistical analysis plan, or whether interim analyses were planned. Those details should not be inferred from the enrollment figure or from the re-calculated planning illustrations.

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.

24-week Double-blind Treatment Period

Reasons for not completing this period:

Extension Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary analysis was performed on the FAS (observed case \[OC\]) with treatment assignment as randomised.

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: The full analysis set (FAS) consisted of all patients who were randomised and treated with at least 1 dose of trial drug and had a baseline HbA1c assessment and at least 1 on-treatment HbA1c assessment during the 24 week double-blind part of the trial.

6. Primary Endpoint

The registry lists the primary outcome as Change of Glycosylated Haemoglobin A1c (Glycosylated Haemoglobin A1c After 24 Weeks of Double-blind Treatment From Baseline), measured over Baseline and 24 week.

The primary endpoint is change in glycosylated haemoglobin A1c (HbA1c) from baseline to Week 24, measured in percentage points. For each participant, the registry defines change as the Week 24 measurement minus the baseline measurement; baseline is the last observed measurement before randomized trial medication began. A negative change therefore represents a lower Week 24 value than baseline, while a positive change represents a higher value.

HbA1c is a continuous measure, so the analysis summarizes average change rather than counting participants who cross a threshold. The registry reports adjusted means, also called least-squares means, with standard errors. Adjustment can account for variables included in a statistical model, but the covariates and full model specification are not reported in the registry record.

As a general statistical matter, a continuous endpoint can preserve information about the magnitude of change across participants, whereas reducing it to categories can discard detail. HbA1c is used in this trial as a measure of glycaemic control. The endpoint alone does not describe every aspect of health, treatment burden, or safety, and it does not establish what an individual participant’s result would be.

7. Results Posted in the Registry

• Empagliflozin 10 mg/Linagliptin 5 mg: mean -0.93 versus 0.21 on control; difference -1.14 (95% CI -1.35 to -0.93), standardized effect d = -1.37; 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 HbA1c From Baseline at Week 52 (Empagliflozin 25 mg/Linagliptin 5 mg Versus Linagliptin 5 mg + Placebo 25 mg)

• 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:
  • Empagliflozin 25 mg/Linagliptin 5 mg: mean -1.10 versus 0.11 on control; difference -1.21 (95% CI -1.45 to -0.97), standardized effect d = -1.46; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Empagliflozin 25 mg/Linagliptin 5 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary HbA1c outcomes at Week 52, including comparisons involving empagliflozin 25 mg/linagliptin 5 mg, placebo, and pooled empagliflozin or placebo groups. The detailed secondary comparison recorded for empagliflozin 25 mg/linagliptin 5 mg versus linagliptin 5 mg plus placebo 25 mg has the same broad direction as the primary result: the estimated change is lower in the combination group. It is a different dose comparison at a later time point, so it should not be treated as a direct replication of the primary endpoint.

Across the primary result and that detailed secondary comparison, the available pattern is directionally consistent for HbA1c change. This does not establish that every secondary endpoint has the same pattern or that the primary estimate applies to all treatment doses. The registry record does not provide enough detailed numerical results in the information to characterize every listed secondary comparison individually. Where a result is not reported in the registry record, it should not be inferred from another endpoint.

Secondary outcomes generally have a supportive or exploratory role, depending on the prespecified analysis plan. Testing multiple outcomes and contrasts creates more opportunities for apparently notable results to arise by chance. Adjustment for multiple testing can help control that risk, but the registry record does not report a multiplicity procedure for these secondary analyses. Their p-values, if considered, should therefore carry less confirmatory weight than a single prespecified primary analysis unless an appropriate testing strategy is documented.

The primary endpoint remains the main basis for interpreting the trial’s stated question. Secondary consistency can add context, but differences in dose, comparator, and assessment time mean the endpoints answer related rather than identical questions.

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

• Change in HbA1c From Week 28 at Week 52 (Empagliflozin 25 mg/Linagliptin 5 mg Only)
• Change in HbA1c From Baseline at Week 52 (All Empagliflozin Versus All Placebo)
• Change in HbA1c From Baseline at Week 52 (Empagliflozin 25 mg/Linagliptin 5 mg Versus Linagliptin 5 mg + Placebo 25 mg)
• Change in HbA1c From Baseline at Week 52 (Empagliflozin 25 mg/Linagliptin 5 mg Versus All Placebo)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry reports least-squares means. In general, a least-squares mean is a model-based estimate of a group average, often adjusted for specified covariates. It can differ from a simple arithmetic mean if the model incorporates covariates or other structure. The registry record identifies the estimate as adjusted but does not report the covariates, model formula, or all fitting details, so those cannot be reconstructed from the posted summary.

What does the mean difference represent?

The mean difference compares the estimated change in the intervention group with the estimated change in the control group. The contrast is defined by subtracting the control-group estimate from the intervention-group estimate. A negative value in this comparison indicates a lower estimated change for the intervention group. Because the endpoint is change from baseline, the contrast describes a between-group difference in average change, not a difference in the groups’ baseline HbA1c values.

The sponsor’s reported analysis is a Mixed Models Analysis and labels its contrast an adjusted mean difference (net). A mixed model is a general modeling approach that can account for relationships among repeated measurements or other structured data, depending on its specification. The registry record does not report enough detail to describe the specific model structure, assumptions, covariates, or missing-data treatment. The sponsor’s point estimate and interval are therefore best interpreted as the results of the reported model, without assuming unlisted features.

What does the standard error describe?

The arm-level results give standard errors for the least-squares means. In general, a standard error describes the sampling uncertainty of an estimated quantity: it indicates how much an estimate would tend to vary across repeated samples under the statistical model. It is not the standard deviation of individual participant values. A smaller standard error generally corresponds to a more precisely estimated mean, although precision also depends on the model and data structure.

The registry’s comparison also gives an unadjusted re-calculation using posted group estimates and standard errors. That calculation is an approximation based on summary statistics rather than a re-fit of the sponsor’s model to participant-level data. The pooled standard deviation and standardized effect listed for the comparison are also recalculated quantities; the pooled spread is marked as approximate. Such standardized quantities can help express an effect relative to variability, but they do not replace the original endpoint scale or the sponsor’s adjusted result.

How should the p-value be read?

A p-value is calculated under a null hypothesis, commonly that the specified group contrast is zero, and describes how often a result at least as extreme as the observed one would arise under that hypothesis and the test’s assumptions. It does not measure the probability that treatment has no effect, and it does not quantify the probability that the finding is due to chance in an everyday sense. The sponsor’s p-value is attached to the mixed-model analysis; the re-calculated p-value is unadjusted and comes from the summary-statistic approximation. They should not be treated as if they were results from the same analysis.

General statistical interpretation also distinguishes statistical evidence from effect size. A small p-value can accompany a small or large estimated difference, depending on the precision and data. Here the mean difference and confidence interval give information about the estimated scale and uncertainty, while the p-value addresses evidence against the model’s null hypothesis. The registry record does not state a clinical-importance threshold for HbA1c change.

What does randomization contribute?

In general, random assignment helps balance both measured and unmeasured participant characteristics across treatment groups on average, reducing confounding in a comparison. It does not guarantee exact balance in any one trial, and it cannot prevent bias arising from missing data, deviations from assigned treatment, measurement, or analysis choices. The registry identifies the study as randomized and says the primary analysis followed randomized treatment assignment. Details about allocation concealment, adherence, and post-randomization treatment changes are not reported in the registry record.

Double masking can reduce the risk that knowledge of assigned treatment influences behavior or outcome assessment. It does not by itself establish that masking remained intact, and the registry record does not provide details on masking procedures or their success. A parallel-group study compares outcomes in separate randomized groups over time; it does not provide a within-person crossover comparison.

Why does the analysis population matter?

The primary population is described as the full analysis set using observed cases, analyzed as randomized. An observed-case analysis uses available outcome measurements rather than imputing missing ones, as far as the registry description indicates. Randomized assignment as the analysis basis preserves the intended group comparison in that respect, but observed-case inclusion can still be affected if availability of measurements is related to outcomes or treatment. The amount and pattern of missing data, reasons for missingness, and any sensitivity analyses are not reported in the registry record.

These distinctions explain why a re-calculation from arm summaries is useful as a check but is not a substitute for the sponsor’s model. The re-calculation does not reproduce adjustments, repeated-measure structure, or other details that may be in the original analysis. No trial-specific statistical features beyond those explicitly reported should be inferred.

11. Confidence Intervals and Precision

The sponsor’s adjusted mean difference for the primary endpoint is -1.14 percentage points, with a 95% confidence interval from -1.36 to -0.91. A confidence interval is a range produced by a statistical procedure that, under its assumptions and repeated use, has the stated coverage. It describes uncertainty in the estimated average contrast; it does not mean that there is a 95% probability that the fixed true effect lies inside this particular interval.

The unadjusted re-calculation gives a mean difference of -1.14 and a confidence interval from -1.352 to -0.928. This interval is based on a simple approximation from the posted summary statistics, not on the sponsor’s mixed model. The two intervals are similar in location and direction, but their endpoints differ. The sponsor’s analysis remains the trial’s reported model-based result; the re-calculation is a separate check.

Both confidence intervals lie below zero, which indicates that the estimated contrast is negative across the ranges reported. Their widths express uncertainty in the average contrast under the corresponding methods. Neither interval captures uncertainty from every possible source, such as model misspecification, missing outcomes, or systematic bias. The registry record does not give a prespecified clinical relevance margin, so the interval cannot by itself determine clinical importance.

Precision is also distinct from individual variability. These intervals concern the estimated group contrast, not the range of changes expected among individual participants. Arm-level standard errors describe uncertainty in the estimated least-squares means; they are not measures of the spread of participant outcomes. General caution is warranted when interpreting precision from an analysis whose full model and missing-data procedures are not reported.

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 planning figures are participants per arm, not total events. They are illustrations based on the observed effect in the posted comparison, rather than the trial’s original sample-size calculation. The registry record does not report the original design assumptions or sample-size justification.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect: 100%, 75%, or 50%. For the primary comparison, the figures are 9 and 12 participants per arm for 80% and 90% power when planning for 100% of the observed effect; 15 and 20 for 75%; and 34 and 45 for 50%.

The 80% power column represents the number of participants per arm the planning calculation indicates would be needed for an 80% chance of rejecting the null hypothesis if the assumed effect and other planning assumptions were true. The 90% column expresses the corresponding planning target for a 90% chance. These are hypothetical design calculations, not evidence about the chance that this completed trial detected an effect. This is not observed power.

Smaller effects are harder to distinguish from random variation, so the planning calculation requires more participants per arm for the smaller fractions. The values are sensitive to the assumed effect and variability, and the observed effect may not be a reliable estimate for planning a new study. They should not be interpreted as the actual design target for this trial or as a substitute for its unreported protocol assumptions.

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 = -1.140; pooled standard deviation σ = 0.830.
2. n = 2 × (1.96 + 0.842)² × 0.830² / -1.140² = 8.3, rounded up to 9 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 <- -1.14                      # observed difference in means
sigma <- 0.829613970867982                     # 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(2453555)
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 = 9 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 15 (80% power), 20 (90% power)
 50% of observed effect: n per arm = 34 (80% power), 45 (90% power)
power.t.test: 9.4 
Simulated power at n = 9 per arm: 0.782 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reports a mixed-model adjusted mean difference of -1.14 percentage points, with a 95% confidence interval from -1.36 to -0.91 and p < 0.001. The summary-statistic re-calculation gives -1.14, with a confidence interval from -1.352 to -0.928 and p < 0.001. The point estimates agree at the precision displayed for the sponsor’s estimate, and both analyses indicate a negative contrast.

The re-calculation is a simple, unadjusted approximation using the posted arm-level means and standard errors. It does not reproduce the sponsor’s mixed-model analysis or its adjustments. Differences in interval endpoints and p-values are therefore expected when methods differ; they do not, on their own, indicate an error. The registry record does not flag a discrepancy between the re-calculation and the reported analysis.

The sponsor’s result is the trial’s reported analysis and should be distinguished from the supplemental recalculation. The latter is useful for checking the broad numerical pattern, but it cannot establish that the sponsor’s model assumptions are correct or recover unreported analysis details. The registry record does not provide a full model specification to allow independent replication of the adjusted estimate.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary Week 24 HbA1c endpoint and lists secondary HbA1c outcomes at Week 52. Multiple comparisons can increase the chance of at least one apparently positive result when each is assessed separately. Statistical methods such as hierarchical testing or adjustment of significance levels can address this issue, but the registry record does not report whether a multiplicity strategy was prespecified or used. The unadjusted secondary results should therefore be interpreted cautiously rather than as independent confirmation.

The primary analysis population is the full analysis set using observed cases, with participants analyzed according to randomized assignment. In general, an observed-case analysis uses the outcome data available for analysis and does not, by that label alone, explain how missing measurements were handled. The registry record does not report the extent or pattern of missing primary outcome data, reasons for missingness, imputation methods, or sensitivity analyses. If missingness is related to treatment or outcome, an observed-case estimate may not represent the full randomized population without additional assumptions.

The registry record also does not report the complete statistical analysis plan, model covariates, assumptions for the mixed model, or details of any interim analyses. These omissions limit assessment of whether analyses were fully prespecified and how robust the estimates are to alternative assumptions. They do not establish that a particular method was or was not used; the details are simply not reported in the registry record.

Randomized treatment assignment in the primary analysis is a relevant strength of the stated approach, but the observed-case qualification means the estimate is not automatically equivalent to an analysis with complete outcomes for every randomized participant. The reported result should be interpreted within these limits, without assuming unreported missing-data or multiplicity procedures.

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: lumbar spinal stenosis (1.1%), oesophageal carcinoma (0.5%), adrenal neoplasm (0.5%), lung neoplasm malignant (0.5%), cerebral haemorrhage (0.5%).

The registry groups safety information as “All Empagliflozin” and “All Placebo.” For serious adverse events, it reports 8 affected among 182 at risk in the all-empagliflozin group, and 1 affected among 93 at risk in the all-placebo group. For other adverse events, it reports 62 affected among 182 at risk and 46 affected among 93 at risk, respectively. These are counts as recorded, not estimates of a causal treatment effect.

Serious adverse events and other adverse events are distinct categories in the registry. Seriousness is a regulatory classification and should not be confused with the number of all symptoms or events. The registry lists serious-event terms including lumbar spinal stenosis at 1.1%, oesophageal carcinoma at 0.5%, adrenal neoplasm at 0.5%, lung neoplasm malignant at 0.5%, cerebral haemorrhage at 0.5%, and glaucoma at 0.5%. The listed percentages do not, by themselves, establish that an event was caused by study treatment.

The registry record does not report death counts in the available safety information. These safety summaries do not establish the comparative safety of the regimens; interpretation would require fuller context, including event definitions, timing, exposure, and adjudication details, which are not reported in the registry record.

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

The primary result describes an average difference in change in HbA1c between randomized groups at Week 24. The sponsor’s model estimates a negative adjusted mean difference, and the reported confidence interval lies below zero. The unadjusted summary-statistic calculation is similar in direction and point estimate. Together, these figures describe the posted statistical comparison; they do not establish what happened to every participant or what the same comparison would produce in another study.

The finding is specific to the trial population and regimen described in the registry: Japanese patients with type 2 diabetes and insufficient glycaemic control after linagliptin treatment, comparing empagliflozin 10 mg with linagliptin 5 mg against linagliptin 5 mg plus placebo 10 mg. The registry’s primary endpoint is measured at Week 24. The separate Week 52 secondary comparison concerns a different empagliflozin dose. Results should not be assumed to apply to other populations, doses, comparators, treatment periods, or outcomes.

A statistically small p-value does not establish clinical importance. The registry record does not report a threshold for a clinically meaningful HbA1c difference, and the estimate does not answer questions about long-term outcomes or the balance of benefits and harms. Safety counts are descriptive and cannot establish causation or provide a complete safety assessment on their own.

The result also depends on the analysis approach. The sponsor reports an adjusted mixed-model comparison, while the recalculation uses posted summary statistics and is unadjusted. The primary analysis uses observed cases in the full analysis set, analyzed as randomized; missing-data details are not reported. These limits matter when judging how precisely and broadly to interpret the estimated group difference.

Accordingly, the registry supports a description of the observed statistical result at the specified endpoint and time. It does not, on its own, settle individual treatment decisions, establish every aspect of clinical value, or replace assessment of the full trial report and other evidence.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint’s time point, treatment contrast, and analysis population need to be read together. The overall study is described as 52 weeks, while the primary HbA1c endpoint is the change from baseline at Week 24. Week 52 outcomes are secondary and include different dose and comparator formulations. Treating those estimates as interchangeable would blur distinct questions.

It also shows the distinction between an adjusted sponsor analysis and an unadjusted calculation from summary statistics. The reported adjusted estimate and the simple recalculation have similar point estimates, but their intervals and p-values are not identical. The recalculation can serve as a numerical check, yet it cannot reconstruct the sponsor’s mixed model or determine the consequences of unreported model choices.

Precision is more informative than a p-value alone. A point estimate gives the scale and direction of the contrast, while a confidence interval conveys uncertainty under the analysis assumptions. Neither fully accounts for potential bias, missing data, or limitations in generalizability. The absence of a reported clinical relevance threshold also means that statistical evidence should not be equated with clinical importance.

Finally, the sample-size illustrations show how planning depends on the assumed effect size and statistical assumptions. They are not evidence of the trial’s original design rationale. The original sample-size justification, missing-data procedures, multiplicity strategy, and full model specification are not reported in the registry record. Recognizing these boundaries is part of interpreting a completed trial responsibly.

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 does not report the original sample-size justification, so the enrollment figure cannot be used to infer the trial’s design target or anticipated effect. The planning illustrations based on the observed effect are not a substitute for that information. The full statistical analysis plan and mixed-model specification are also not reported, limiting independent assessment of model assumptions and covariate adjustment.

The primary analysis is described as an observed-case analysis in the full analysis set. The registry record does not report missing outcome counts, reasons for missingness, or sensitivity analyses, so the extent to which missing data could influence the estimate cannot be assessed from this record. It also does not report a multiplicity strategy for the secondary outcomes, making those results less suitable as standalone confirmatory evidence.

Generalizability is bounded by the population and regimens described: Japanese patients with type 2 diabetes and insufficient glycaemic control after linagliptin treatment, with specific empagliflozin and placebo comparisons. The registry record does not provide further eligibility details in the information available for this analysis. Results should not be assumed to transfer unchanged to populations or treatment settings not represented in the trial.

The safety summary is limited to grouped adverse-event counts and selected serious-event terms. The available record does not report deaths, detailed event timing, treatment exposure, or additional context needed to assess causality and comparative risk. The primary endpoint is a measure of HbA1c change at Week 24; it does not address every outcome relevant to long-term health or treatment burden.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Empagliflozin Add on to Linagliptin Study in Japanese Patient With Type 2 Diabetes Mellitus — NCT02453555.
• Registry record last updated 2019-02-15; status last verified 2018-09.
• Results first posted 2019-02-15.
• 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

NCT02453555 is a completed Phase III randomized, double-blind, parallel-group study sponsored by Boehringer Ingelheim. The registry reports enrollment of 275 and describes a 52-week study in Japanese patients with type 2 diabetes. The primary endpoint was change in HbA1c from baseline to Week 24, analyzed in the full analysis set using observed cases and randomized treatment assignment.

The sponsor’s mixed-model analysis reports an adjusted mean difference of -1.14 percentage points, with a 95% confidence interval from -1.36 to -0.91 and p < 0.001. A simple unadjusted re-calculation gives a similar point estimate, with an approximate confidence interval and p-value based on the posted summaries. The registry record does not report the original sample-size rationale, detailed missing-data procedures, multiplicity strategy, or complete model specification.