Empagliflozin (BI 10773) Dose Finder Study in Japanese Patients With Type 2 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Empagliflozin (BI 10773) Dose Finder Study in Japanese Patients With Type 2 Diabetes Mellitus (NCT01193218), a randomized phase 2 study. The primary outcome is Change From Baseline in HbA1c After 12 Weeks of Treatment..

2. Clinical Question

3. Trial Design

This completed Phase 2 study was a randomised, double-blind, parallel-group trial sponsored by Boehringer Ingelheim. It enrolled 547 participants with type 2 diabetes. The registry record describes treatment as monotherapy for patients whose glycaemic control remained insufficient despite diet and exercise. The study began in 2010-09, and primary completion was recorded in 2012-06.

During the initial 12-week period, participants were assigned to once-daily placebo or one of four BI 10773 doses: 5 mg, 10 mg, 25 mg, or 50 mg. The primary endpoint was assessed at 12 weeks. The registry record also describes a 40 week randomised extension to assess longer-term safety for BI 10773 at 10 mg and 25 mg. These periods address different questions: the primary efficacy comparison is focused on the initial 12 weeks, while the extension contributes longer-term safety information.

The posted primary endpoint results include 109 or 110 participants in each treatment group, with 109 in the placebo group. The reported analysis population is the full analysis set. The record identifies the design as double-blind but does not report the operational details of masking, the randomisation sequence, allocation concealment, or the rules governing assignment to the extension. Those details are not reported in the registry record.

The official study title specifies comparison with placebo and describes the study as a dose-finding study in Japanese patients. Enrollment across the trial should not be confused with the number contributing to any one outcome analysis: the posted endpoint groups have their own analysis counts, and the secondary binary outcome has different counts. The registry record does not give a detailed account of participant flow or reasons for missing outcome observations.

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.

Only the first 6 of 8 groups are shown.

0-12 Weeks

Reasons for not completing this period:

12-52 Weeks

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS)

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in HbA1c After 12 Weeks of Treatment., measured over baseline and 12 weeks.

The primary endpoint is change from baseline in HbA1c after 12 weeks of treatment, reported as a least-squares mean in the full analysis set. HbA1c is used to assess glycaemic control over time. Looking at change, rather than only the end-of-treatment value, describes how the measure shifted from each participant’s starting point. Comparing changes between groups helps distinguish the pattern in the assigned treatment groups from change observed in the placebo group over the same period.

The posted arm estimates are 0.3 for placebo, -0.42 for 5 mg, -0.4 for 10 mg, -0.65 for 25 mg, and -0.61 for 50 mg, in percentage of HbA1c. Negative estimates indicate a decrease from baseline, while the placebo estimate is positive. The registry record reports standard errors alongside the arm estimates; a standard error describes uncertainty around an estimated mean, not the spread of individual participants’ measurements.

The endpoint is useful for comparing groups at a specified follow-up, but it is not by itself a complete account of overall clinical outcomes or safety. The registry record gives 12-week results for this primary measure. It does not report a longer-term primary efficacy assessment in the results.

7. Results Posted in the Registry

• Empa 5mg (12 Week): mean -0.42 versus 0.30 on control; difference -0.72 (95% CI -0.97 to -0.47), standardized effect d = -0.76; z-test p = <0.001.
• Empa 10mg (12 Week): mean -0.40 versus 0.30 on control; difference -0.70 (95% CI -0.95 to -0.45), standardized effect d = -0.74; z-test p = <0.001.
• Empa 25mg (12 Week): mean -0.65 versus 0.30 on control; difference -0.95 (95% CI -1.20 to -0.70), standardized effect d = -1.01; z-test p = <0.001.
• Empa 50mg (12 Week): mean -0.61 versus 0.30 on control; difference -0.91 (95% CI -1.16 to -0.66), standardized effect d = -0.97; 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.

Occurrence of Treat to Target Efficacy Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Empa 5mg (12 Week): 26.2% (28/107) versus 2.8% (3/106) on control; risk difference 23.3 percentage points (95% CI 14.4 to 32.2), risk ratio 9.25 (2.90–29.49); unadjusted two-proportion z-test p = <0.001.
  • Empa 10mg (12 Week): 19.0% (20/105) versus 2.8% (3/106) on control; risk difference 16.2 percentage points (95% CI 8.1 to 24.4), risk ratio 6.73 (2.06–21.97); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Empa 5mg (12 Week) 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 proportion with the event is statistically higher for Empa 10mg (12 Week) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in 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:
  • Empa 5mg (12 Week): mean -22.65 versus 4.06 on control; difference -26.71 (95% CI -34.82 to -18.60), standardized effect d = -0.87; z-test p = <0.001.
  • Empa 10mg (12 Week): mean -25.28 versus 4.06 on control; difference -29.34 (95% CI -37.17 to -21.51), standardized effect d = -0.99; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Empa 5mg (12 Week) 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 Empa 10mg (12 Week) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results cover two different kinds of outcomes. Treat-to-target efficacy response is binary and is reported as a percentage of participants, while change from baseline in fasting plasma glucose is continuous. Across the active dose groups, the response percentages are higher than the placebo percentage, and the FPG mean changes are lower than placebo. This overall pattern is directionally consistent with the primary HbA1c comparisons, in which the active-group changes and placebo comparison estimates fall in the same direction.

The secondary outcomes broaden the description of the 12-week results, but they do not replace the primary endpoint. A response percentage addresses whether a stated target criterion was reached, whereas an average change in a continuous measure describes the group’s estimated shift. FPG is another continuous measure, distinct from HbA1c. These endpoints can provide complementary evidence, but they are not interchangeable and do not establish the same outcome.

The registry reports logistic regression odds ratios for the treat-to-target outcome in the 5 mg and 10 mg comparisons, and ANCOVA results for FPG in those same two comparisons. The registry does not post sponsor-reported comparisons for every active dose on these secondary outcomes. In particular, the presence of arm-level outcome summaries across more groups does not imply that the same inferential analysis was reported for all doses.

Secondary results generally carry less weight than a prespecified primary result because they may involve additional outcomes, analyses, and comparisons. When many hypotheses are examined, the chance of at least one apparently notable result arising by chance can increase unless the analysis plan accounts for multiplicity. Whether multiplicity was controlled for these secondary analyses is not reported in the registry record. The secondary findings should therefore be treated as supportive descriptions of the posted data, with attention to their analysis coverage and uncertainty, rather than as independent confirmation free of qualification.

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

• Occurrence of Treat to Target Efficacy Response
• Change From Baseline in FPG

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant’s HbA1c change is measured on a numeric scale. The registry record reports group least-squares means and standard errors, then presents sponsor analyses comparing each active dose with placebo. The sponsor used ANCOVA and reported mean differences in final values, 95% confidence intervals, and p-values. ANCOVA is a general method for comparing groups while accounting for covariates included in a model. Which covariates were included, and other details of the sponsor’s model, are not reported in the registry record.

What does a mean difference represent?

A mean difference expresses the estimated separation between two group means on the endpoint’s scale. For these comparisons, a negative value indicates a lower estimated HbA1c result in the BI 10773 group relative to placebo. It is distinct from each group’s own change from baseline. The interpretation also depends on the outcome definition and timeframe: these estimates concern the change after 12 weeks, not a later assessment.

The re-calculations use the posted group summaries to form simple, unadjusted comparisons. Because the posted arm results include standard errors rather than standard deviations, the re-calculation estimates variability from those standard errors. That is an approximation and does not reproduce the sponsor’s ANCOVA model. A standard error measures precision of an estimated group mean; a standard deviation describes variability among individual observations. These quantities answer different questions, and treating one as the other would mischaracterize the summaries.

Why do the sponsor and re-calculated results differ in detail?

The sponsor’s ANCOVA and the simple re-calculation need not have identical confidence limits or p-values. ANCOVA can account for model covariates, while the re-calculation is an unadjusted comparison built from summary statistics. In this record, the point estimates are very similar, and both sets of comparisons point in the same direction. The sponsor’s estimates and intervals remain the appropriate reference for the trial’s own analysis; the re-calculation is a check based on the posted summaries, not a substitute for the sponsor’s model.

For a binary outcome, such as whether a participant reached a target response, the quantity of interest is a proportion or a contrast between proportions. The registry reports logistic regression odds ratios for two comparisons on that secondary endpoint. An odds ratio compares odds, not probabilities, and should not be read as a direct multiple of the percentage of participants meeting the response criterion. The registry also reports percentages and confidence intervals by arm. The exact definition of the target response is not reported in the registry record.

The other secondary endpoint, change from baseline in fasting plasma glucose (FPG), is continuous and is reported in mg/dL. The sponsor used ANCOVA for its posted comparisons. The interpretation of a mean difference is similar to that for HbA1c: it describes an estimated between-group contrast on the outcome’s scale. It does not by itself show how each individual’s result changed.

What does over-dispersion mean in general?

In general, over-dispersion means observed variability is greater than a statistical model expects. It can make standard errors too small if a model’s assumptions do not account for the extra variability, which can in turn make confidence intervals too narrow and p-values too small. The registry record does not report an over-dispersion assessment or a related adjustment for these analyses, so no claim about over-dispersion in this trial is warranted.

Randomisation supports a group comparison by distributing measured and unmeasured characteristics through assignment on average, but the registry’s outcome summaries do not reveal whether every baseline characteristic was balanced. The exact randomisation procedure, stratification factors, model covariates, and handling of deviations from assigned treatment are not reported in the registry record. The result should therefore be described using the reported analysis rather than assumptions about its implementation.

11. Confidence Intervals and Precision

A confidence interval gives a range of values compatible with the data and the analysis method, while reflecting sampling uncertainty. It is not a guarantee that the true value lies in the interval, nor does it describe the range of individual participant responses. The sponsor reported 95% confidence intervals for the four primary comparisons. Those intervals are entirely on the negative side of zero, and each is relatively close to its point estimate. Their limits communicate both the direction and the precision of the estimated between-group differences under the sponsor’s model.

For the 5 mg comparison, the sponsor estimate is -0.72 with a 95% confidence interval from -0.87 to -0.57. For 10 mg, the estimate is -0.70 and the interval is -0.85 to -0.55. For 25 mg, the estimate is -0.95 and the interval is -1.10 to -0.80. For 50 mg, the estimate is -0.91 and the interval is -1.06 to -0.76. These intervals show uncertainty around each separate placebo comparison; they are not intervals for comparisons between active doses.

The arm-level standard errors are 0.09 for all five primary endpoint groups. A standard error is a measure of the uncertainty of an estimated mean, not a description of participant-to-participant variation. The registry record does not post confidence limits for the arm-level means, but it does provide confidence intervals for the sponsor’s between-group analyses.

Precision should be considered alongside the point estimates and analysis context. Narrower intervals indicate greater precision under the stated analysis, but they do not settle whether an effect matters clinically. The registry record does not identify a clinical-importance threshold. It also does not report a multiplicity adjustment, so the confidence intervals and p-values should be understood as the reported comparisons rather than as evidence that an overall family of tests has been controlled at a specified error rate.

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 event counts. They are illustrations based on the observed effect, not the original trial’s design assumptions. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original sample-size justification and its assumptions are not reported in the registry record.

The 80% power column means that, under those planning assumptions and for the chosen effect size, a study of the stated size would have an 80% chance of detecting an effect at the specified significance level. The 90% power column uses a higher target chance of detecting that effect. These are planning concepts, not guarantees about the result of a future study. The figures are not observed power for this completed trial.

Each set of planning figures is tied to a particular comparison and an assumed fraction of that comparison’s observed effect. “100% of the observed effect” uses the full estimated effect as the planning target; “75%” and “50%” use smaller targets. Smaller effects are generally harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm. For example, for the 5 mg primary comparison, planning for 100% of the observed effect gives 27 participants per arm for 80% power, whereas planning for 50% gives 108 participants per arm for 80% power. Those values illustrate the effect-size relationship and should not be mistaken for enrollment recommendations or the trial’s actual design rationale.

The calculations are based on a two-arm comparison and should be read in that context. They do not represent a complete sample-size plan for a multi-arm trial with multiple endpoints or comparisons. They also do not account for design features or adjustments that are not included in the stated planning assumptions. The sample-size justification used by the investigators is not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.720; pooled standard deviation σ = 0.942.
2. n = 2 × (1.96 + 0.842)² × 0.942² / -0.720² = 26.9, rounded up to 27 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.72                      # observed difference in means
sigma <- 0.94179013776662                     # 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(1193218)
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 = 27 (80% power), 36 (90% power)
 75% of observed effect: n per arm = 48 (80% power), 64 (90% power)
 50% of observed effect: n per arm = 108 (80% power), 144 (90% power)
power.t.test: 27.9 
Simulated power at n = 27 per arm: 0.793 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analyses used ANCOVA and give a mean difference, a 95% confidence interval, and a p-value for each dose versus placebo. The sponsor estimates are -0.72 for 5 mg, -0.70 for 10 mg, -0.95 for 25 mg, and -0.91 for 50 mg. Each reported p-value is < 0.001. The sponsor’s confidence intervals are -0.87 to -0.57, -0.85 to -0.55, -1.10 to -0.80, and -1.06 to -0.76, respectively.

The simple re-calculations from the posted summaries produce point estimates of -0.72, -0.7, -0.95, and -0.91 for the same comparisons. The re-calculated p-values are each <0.001. Similarity in point estimates supports consistency between the posted group summaries and the reported comparisons, but the procedures are not identical: the re-calculations are unadjusted and use approximate variability derived from the standard errors, while the sponsor reports ANCOVA.

The registry record does not flag a discrepancy between the sponsor analysis and the re-calculation. The sponsor’s model-based results are the primary source for describing the trial’s analysis. The re-calculation is best treated as a supplementary check and not as a replacement for the sponsor’s model, since the model details and covariate adjustments are not fully reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record reports a primary endpoint and two secondary outcomes, along with multiple dose-versus-placebo comparisons. It presents p-values for the sponsor’s primary comparisons and selected secondary comparisons. Whether the trial’s statistical plan adjusted for multiple comparisons, and what family of tests such an adjustment would cover, is not reported in the registry record. The posted p-values should therefore be read as the reported results, not assumed to control the chance of a false positive across all outcomes and dose comparisons.

The record does not report whether interim analyses were planned or conducted, whether any stopping rules were used, or whether the endpoint hierarchy included formal testing procedures. These details matter when interpreting a set of related tests, but should not be inferred from the p-values alone. Similarly, whether outcomes were selected or reported according to a prespecified hierarchy is not reported in the registry record.

The primary endpoint population is identified as the full analysis set. The record does not define that population, describe how participants with missing measurements were treated, or state whether imputation or another missing-data method was used. The analysis population and missing-data procedures are important because the result may depend on which participants contribute outcome data and how unavailable values are handled. Participant flow, reasons for missing data, and sensitivity analyses are not reported in the registry record.

The sponsor identifies ANCOVA as the method for the primary comparisons, but the covariates and model specification are not reported. The registry record also does not report details on model diagnostics, adjustments for departures from assumptions, or a full statistical analysis plan. These gaps do not negate the posted estimates; they limit how fully the analysis can be independently reconstructed and how confidently the reader can assess the role of unreported analytical choices.

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: pharyngitis (0.9%), viral infection (0.9%), colon cancer (0.9%), diffuse large b-cell lymphoma (0.9%), gastric cancer (0.9%).

The registry reports serious adverse event counts and the numbers at risk for the initial 12-week groups and for extension-related groups. In the 12-week placebo group, 3 of 109 participants were recorded as affected; the counts were 0 of 110 for 5 mg, 0 of 109 for 10 mg, 3 of 109 for 25 mg, and 1 of 110 for 50 mg. For the randomized 52-week groups, the posted counts are 3 of 109 for 10 mg and 8 of 109 for 25 mg. The “with at least one dose” 52-week groups have counts of 8 of 267 for 10 mg and 15 of 265 for 25 mg.

These counts belong to different follow-up groupings and denominators, so comparisons across them should take the period and population labels into account. They are descriptive counts, not evidence by themselves that one group has a higher or lower underlying risk. The registry record lists several serious-event terms at 0.9% each, but does not assign those listed terms to specific treatment groups in the posted summary. Death counts are not reported in the registry record. The posted serious-event figures do not provide a complete safety profile or establish causation.

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

The primary posted results show that, after 12 weeks, each BI 10773 dose group had a lower estimated change in HbA1c than the placebo group. The sponsor’s ANCOVA estimates are negative for all four dose comparisons, their 95% confidence intervals exclude zero, and the reported p-values are < 0.001. The re-calculations from group summaries are close to the sponsor’s estimates, while remaining distinct, unadjusted calculations.

These findings describe the trial’s results for the primary endpoint, the analysis population, and the 12-week treatment period. They do not establish the comparative effect of one active dose versus another: the reported primary comparisons are each against placebo. The fact that some dose estimates are numerically more negative than others does not establish a dose-response relationship. Direct active-dose comparisons and an analysis designed to assess dose response are not reported in the registry record.

The results do not by themselves establish clinical importance. The registry record does not report a threshold for a clinically meaningful HbA1c difference, and statistical significance is not the same as clinical relevance. The primary endpoint is also only one measure. The secondary results and safety summaries contribute additional context, but do not transform the primary endpoint into evidence about every outcome or every duration of treatment.

The trial enrolled Japanese patients with type 2 diabetes described as having insufficient glycaemic control despite diet and exercise. The findings should not automatically be generalized to populations or circumstances not described in the record. The registry record does not provide the full eligibility criteria, detailed participant characteristics, or complete information on missing outcomes and analysis choices. Those limits constrain interpretation of both applicability and precision.

No treatment recommendation follows from these statistical summaries. They report group-level estimates and their uncertainty, not an individualized prediction or a complete balance of benefits and harms. Safety counts are descriptive, and the longer extension addresses safety follow-up rather than extending the primary efficacy endpoint beyond its stated 12-week timeframe.

18. Why This Trial Matters Statistically

Statistically, this study is informative because it evaluates several doses against a common placebo group and reports a continuous primary endpoint at a specified follow-up. The shared comparator makes the dose-specific estimates interpretable in relation to the same control condition, while the parallel-group randomized design provides the framework for comparing assigned groups. The double-blind design is also part of the trial’s stated structure, although the operational details of masking are not reported in the registry record.

The record provides both group-level least-squares means and sponsor-reported ANCOVA contrasts with confidence intervals. That combination makes it possible to distinguish within-group change from between-group differences and to consider precision rather than relying only on p-values. The unadjusted re-calculations from the posted summaries offer a further consistency check, while their approximate variability and lack of model adjustment show why a reconstruction should not be confused with the sponsor’s analysis.

The trial also illustrates why multiple dose comparisons and secondary outcomes require careful reading. A set of apparently precise, statistically significant comparisons does not by itself answer whether multiplicity was addressed, whether a particular dose is superior to another, or whether the observed magnitude is clinically important. The registry record leaves these issues unresolved or does not report them.

Finally, efficacy and safety results concern different timeframes. The primary endpoint is assessed at 12 weeks, while the record includes a 40 week randomised extension for longer-term safety assessment. Keeping those questions distinct helps prevent a short-term efficacy estimate from being mistaken for a longer-term efficacy result, or descriptive safety counts from being interpreted as conclusive comparisons.

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 primary efficacy results cover 12 weeks, and the registry record does not provide a longer-term primary HbA1c comparison. The extension is described as a safety assessment for the 10 mg and 25 mg doses. It therefore does not establish the persistence of the primary endpoint pattern over the extension period.

The record gives only limited detail for reconstructing the trial’s analysis. The sponsor reports ANCOVA, but the model covariates and other specification details are not reported. The FAS is named but not defined. Handling of missing outcome data, participant flow, and sensitivity analyses are also not reported. The re-calculation uses approximate variability based on reported standard errors and is unadjusted, so it cannot resolve these gaps or reproduce the sponsor’s model.

There are four dose-versus-placebo primary comparisons, as well as secondary outcomes. Multiplicity procedures are not reported in the registry record. The sponsor-reported intervals and p-values should be interpreted as the posted analyses, without assuming a family-wise adjustment. The registry also does not report a prespecified threshold for clinical importance, limiting interpretation of the magnitude in clinical rather than statistical terms.

The primary comparisons do not directly compare active doses. Consequently, relative ordering of the point estimates cannot establish that one dose is more effective than another, nor does it demonstrate a dose-response relationship. The secondary outcome analyses are not posted for every active dose in the same way, and the registry does not provide a full statistical plan explaining that coverage.

The safety information is presented as counts across groups with different follow-up labels and denominators. The record does not report deaths in these summaries, and listed serious-event terms are not linked to treatment groups in the posted term summary. These limitations make the safety counts descriptive rather than a complete comparative assessment. Generalizability is also limited by the population description; detailed baseline characteristics and full eligibility criteria are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Empagliflozin (BI 10773) Dose Finder Study in Japanese Patients With Type 2 Diabetes Mellitus — NCT01193218.
• Registry record last updated 2014-06-17; status last verified 2014-05.
• Results first posted 2014-06-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed Phase 2 study enrolled 547 Japanese patients with type 2 diabetes and compared once-daily BI 10773 at 5 mg, 10 mg, 25 mg, and 50 mg with placebo during a 12-week treatment period. The study was randomised, double-blind, and parallel-group. Its primary endpoint was change from baseline in HbA1c, analyzed in the full analysis set.

The sponsor reported ANCOVA mean differences versus placebo of -0.72, -0.70, -0.95, and -0.91 for the four doses, with 95% confidence intervals excluding zero and p-values < 0.001. The registry record also describes a 40 week randomised extension intended to assess longer-term safety at 10 mg and 25 mg, and posts two secondary outcomes and safety counts. Details of multiplicity control, missing-data handling, and the complete statistical model are not reported in the registry record.