Monotherapy Study of MP-513 in Patients With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Monotherapy Study of MP-513 in Patients With Type 2 Diabetes (NCT00998881), a randomized phase 3 study. The primary outcome is Change From Baseline in HbA1c at Week 12.

2. Clinical Question

The principal statistical contrast is the difference in least-squares mean change in HbA1c between the teneligliptin and placebo groups. A negative contrast means the estimated change was lower in the teneligliptin group under the registry’s outcome coding. The estimates describe this study population and follow-up period; they do not, on their own, establish how the treatment would compare in other populations or over other durations.

The registry also lists fasting plasma glucose, postprandial plasma glucose area under the curve, and 2-hour postprandial plasma glucose as secondary outcomes. Those measures provide related information about glucose outcomes, but HbA1c is the designated primary endpoint. The study record does not report a broader clinical question about long-term outcomes.

3. Trial Design

This was a Phase III, randomized, quadruple-masked, parallel-group study comparing teneligliptin 20 mg with matching placebo in Japanese patients with type 2 diabetes. The registry describes the study as double-blind in its official title and lists quadruple masking in its design fields. Both groups took tablets orally once daily. The stated administration period and primary endpoint timeframe were 12 weeks.

The registry lists enrollment of 203 and a completed study status. The recorded start was 2009-09 and primary completion was 2010-06. The primary endpoint analysis included 104 placebo participants and 99 teneligliptin participants. Its analysis population was defined as patients who received at least one dose and had at least one efficacy measurement after randomization. The primary outcome used last observation carried forward: the last observed post-baseline value during the double-blind period was carried forward.

The primary endpoint was analyzed using analysis of covariance, with treatment as a fixed effect and baseline HbA1c as a covariate. The registry reports least-squares means and standard errors for the group changes. These are model-based estimates rather than simple unadjusted averages, because the stated model accounts for baseline HbA1c.

The registry record does not report the original sample-size justification, the trial’s planned power, or the assumptions used in its original design. Details of sequence generation, allocation concealment, adherence, and any interim analyses are not reported in the registry record. The record also does not describe a formal multiplicity strategy for the secondary endpoints. Such missing design information should not be inferred from the posted results or from planning calculations based on the observed effects.

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: The full analysis set, consisting of all type 2 diabetic patients, who received at least one dose of study drug and who had at least one efficacy data after randomization. Analysis based on last observation carried forward, where the last postbaseline double-blind observed value was carried forward and used for Week 12 where data was missing.

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 at Week 12, measured over 12 weeks.

The primary endpoint is change from baseline in HbA1c at Week 12, measured in percent. HbA1c reflects glucose bound to hemoglobin, and the registry defines the measure as a percentage of the absolute maximum that can be bound. The outcome is expressed as change, so a value below zero represents a decrease from the baseline measurement, while a value above zero represents an increase.

HbA1c is used as a continuous measure of glycemic status. In general, continuous endpoints retain information about the size and direction of changes across the measured scale rather than reducing results to categories. That can make estimated average changes useful for comparing groups, while still requiring attention to variability and uncertainty.

The registry reports least-squares mean changes, derived from an analysis of covariance model with treatment as a fixed effect and baseline HbA1c as a covariate. This adjustment accounts statistically for the measured baseline HbA1c when estimating group means. It does not mean that every other possible difference between participants has been adjusted for. The reported analysis population and last-observation-carried-forward approach also shape what the estimates represent.

The endpoint was measured at Week 12; it therefore describes a short-term change over the study’s stated period. The registry does not report a threshold for a clinically important HbA1c change or a longer-term HbA1c outcome. Statistical differences in an endpoint should consequently be interpreted as evidence about the measured outcome and timeframe, not as a complete account of clinical benefit or long-term effects.

7. Results Posted in the Registry

• Teneligliptin 20 mg: mean -0.62 versus 0.17 on control; difference -0.79 (95% CI -0.93 to -0.65), standardized effect d = -1.57; 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 From Baseline in Fasting Plasma Glucose at Week 12

• 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:
  • Teneligliptin 20 mg: mean -19.20 versus -0.20 on control; difference -19.00 (95% CI -23.99 to -14.01), standardized effect d = -1.05; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Teneligliptin 20 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Areas Under the Curve From 0 to 2 h (AUC0-2h) for Postprandial Plasma Glucose at Week 12

• 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:
  • Teneligliptin 20 mg: mean -73.12 versus 0.22 on control; difference -73.35 (95% CI -86.75 to -59.94), standardized effect d = -1.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Teneligliptin 20 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in 2-hour Postprandial Plasma Glucose at Week 12

• 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:
  • Teneligliptin 20 mg: mean -47.90 versus -3.20 on control; difference -44.70 (95% CI -54.54 to -34.86), standardized effect d = -1.28; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Teneligliptin 20 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The three secondary glucose outcomes show a consistent overall direction relative to placebo: the estimated changes and contrasts are negative for teneligliptin. This pattern aligns directionally with the primary HbA1c comparison. Taken together, the secondary measures provide related evidence about glucose outcomes at Week 12, rather than an unrelated set of endpoints.

The secondary outcomes assess different aspects of glucose measurement. Fasting plasma glucose captures a fasting measurement; postprandial measures concern glucose after a meal, including a two-hour assessment and an area-under-the-curve measure. Because the outcomes are related, consistent directions can add context, but they should not be treated as fully independent replications of the primary finding.

The registry lists unadjusted p-values of <0.001 for the secondary comparisons. No multiplicity adjustment or hierarchy for testing these endpoints is reported in the registry record. When several outcomes are examined, unadjusted tests do not account for the greater opportunity to observe a small p-value across the set. As a result, the secondary results carry less confirmatory weight than a primary endpoint with a prespecified testing plan would carry.

The record lists the endpoint estimates, but reports no separate analysis records for the secondary outcomes. The standard errors and comparison estimates are posted, while the analysis population and missing-data handling are not described with the same detail as for the primary endpoint. Those limitations make the secondary results useful as supporting descriptions, but not a substitute for a fully reported multiplicity strategy and analysis plan.

The secondary outcomes should therefore be read as a coherent directional pattern that is compatible with the primary result, while keeping the distinctions between endpoints, analysis details, and multiplicity in view. The record does not establish whether the study was designed or powered to make definitive claims about each secondary measure individually.

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

• Change From Baseline in Fasting Plasma Glucose at Week 12
• Change From Baseline in the Areas Under the Curve From 0 to 2 h (AUC0-2h) for Postprandial Plasma Glucose at Week 12
• Change From Baseline in 2-hour Postprandial Plasma Glucose at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, and the registry reports least-squares mean changes with standard errors. The stated method is analysis of covariance, or ANCOVA. In general, ANCOVA estimates group means while adjusting for a measured baseline covariate. Here, treatment is the fixed effect and baseline HbA1c is the covariate. The resulting least-squares means are model-based estimates, not simply the arithmetic means of observed changes without adjustment.

What does baseline adjustment do?

In general, baseline adjustment can account for variation associated with the starting value of the outcome. It estimates the treatment-group comparison conditional on the baseline HbA1c values represented in the model. It does not adjust for unmeasured characteristics, nor does it establish that every possible imbalance between groups has been removed. The record does not provide additional model details such as diagnostics or other covariates, so none should be assumed.

The primary analysis population is described as the full analysis set. It consists of patients with at least one dose of study drug and at least one efficacy measurement after randomization. This definition is narrower than simply counting everyone enrolled or randomized, because it requires post-randomization treatment exposure and efficacy data. The primary group estimates are based on 104 placebo participants and 99 teneligliptin participants. The registry does not report a separate intention-to-treat analysis or give reasons for any exclusions from the analysis population.

How should last observation carried forward be understood?

The primary analysis used last observation carried forward. In general, this approach fills a missing later measurement with the last observed post-baseline value during the double-blind period. It creates an analysis value for a later assessment, but it relies on an assumption that the carried-forward value is a reasonable stand-in for the unobserved value. That assumption may not represent what would have happened after the last measurement. The registry does not report the amount or pattern of missing data or a sensitivity analysis using other missing-data methods.

The displayed group standard errors describe precision of the estimated means under the analysis, not individual-level variability. A standard error generally becomes smaller when estimates are more precise, but it should not be confused with a standard deviation. The registry’s primary outcome labels the dispersion as standard error. The comparison statistics also include an approximate pooled standard deviation used for standardized-effect and planning calculations; that quantity is reconstructed approximately from the posted standard errors, rather than reported as the trial’s directly observed standard deviation.

What do the comparison statistics represent?

The contrast is the estimated mean change for teneligliptin minus the estimated mean change for placebo. Its negative sign indicates a lower estimated change for teneligliptin under that subtraction order. The comparison interval describes a range of values compatible with the estimate under the calculation used. The record does not state the confidence level associated with this interval. The accompanying p-value is unadjusted and does not reflect correction for multiple endpoint testing.

The comparison values are simple, unadjusted recalculations from the posted summary statistics. They are not a replacement for a sponsor-reported inferential analysis. The registry supplies the primary ANCOVA description and group least-squares means, but no separate sponsor-reported comparison analysis is listed in the record. The discrepancy flag is false, so there is no stated conflict between the recalculation and the posted summaries.

Why do planning calculations use different assumptions?

In general, a sample-size calculation estimates how many participants would be needed to detect a specified effect with a chosen statistical power and significance level. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the groups, and a normal approximation. It considers effects stated as fractions of the observed effect. These are planning assumptions for an illustration, not evidence about the assumptions used to design this trial.

The planning values depend on the estimated effect and variability used as inputs. Because those inputs come from the observed results, the calculations are sensitive to how well those results estimate what might be seen in a future study. Smaller target effects require more participants under the same general planning framework. These figures are not observed power and do not describe the probability that the completed trial’s result is true.

For secondary outcomes, the registry lists estimates and unadjusted comparisons but no separately reported analysis records. In general, testing multiple outcomes can increase the chance of at least one apparently unusual result if no adjustment is used. Since the record does not state a multiplicity plan, the strength of evidence across the secondary endpoints cannot be judged as though they were a single prespecified test family with a known correction. The reported secondary estimates remain useful descriptively, but their inferential status is less clear.

11. Confidence Intervals and Precision

The primary contrast is -0.79, with an interval from -0.929 to -0.651. Its position below zero indicates that the estimated difference is consistently negative over the interval’s reported bounds. The registry does not state the confidence level associated with this interval, so that level should not be assumed. The interval is based on the recalculated comparison from posted summary statistics, not a separately listed sponsor-reported contrast analysis.

An interval is useful because it conveys more than a single point estimate. In general, it shows a range of values compatible with the data and calculation under the interval’s assumptions. A narrower interval indicates greater statistical precision for that estimate than a wider interval would, but precision is not the same as freedom from bias. The interval does not account automatically for missing-data assumptions, limitations in who was studied, or unreported analysis choices.

The standard errors for the primary group means are each 0.05. These quantify uncertainty around the estimated means, rather than the amount of variation among individual participants. The registry’s use of ANCOVA means that the group estimates reflect the stated baseline adjustment. The interval for the between-group contrast should be interpreted as uncertainty around that comparison, not as a prediction interval for individual outcomes.

The unadjusted p-value of <0.001 indicates that the observed comparison is not readily compatible with a zero contrast under the unadjusted calculation and its assumptions. It does not quantify the probability that the treatment effect is real, and it does not measure clinical importance. Because the registry does not report the confidence level or a multiplicity procedure, those details should remain explicit uncertainties when interpreting the apparent precision.

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 planning illustrations based on the observed effect, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and a target effect defined as a stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the calculation model are appropriate. The 90% power column uses a higher probability of detecting that same specified effect, and therefore generally calls for more participants. These are theoretical planning probabilities for a hypothetical study, not probabilities that the current study’s finding is correct.

Rows representing 100%, 75%, and 50% of the observed effect illustrate how the required sample size changes as the target effect changes. A smaller target effect is harder to distinguish from random variation under the same assumptions, so it requires more participants. This relationship is visible across the planning estimates for the primary endpoint and the secondary outcomes. The values are sensitive to the observed estimates and should not be treated as a recommendation for a future trial without considering its own design, population, endpoint, and assumptions.

This is not observed power. It is a prospective-style calculation using the observed effect as an input, and it does not revise the strength of evidence from the completed study.

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 = -0.790; pooled standard deviation σ = 0.504.
2. n = 2 × (1.96 + 0.842)² × 0.504² / -0.790² = 6.4, rounded up to 7 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 <- -0.79                      # observed difference in means
sigma <- 0.503890337907779                     # 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(998881)
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 = 7 (80% power), 9 (90% power)
 75% of observed effect: n per arm = 12 (80% power), 16 (90% power)
 50% of observed effect: n per arm = 26 (80% power), 35 (90% power)
power.t.test: 7.5 
Simulated power at n = 7 per arm: 0.771 (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. Multiplicity, Missing Data and Analysis Populations

The registry identifies HbA1c change at Week 12 as the primary endpoint and lists three secondary glucose outcomes. It does not report a multiple-testing adjustment, a gatekeeping sequence, or another formal procedure for controlling error across these outcomes. Therefore, the reported secondary p-values are unadjusted and should not be interpreted as if the registry documented a family-wise confirmatory testing plan.

Multiplicity matters because repeated statistical tests create multiple opportunities to obtain results that appear unusual by chance. In general, adjustments can control the overall false-positive risk across a defined set of tests, but the appropriate method depends on which outcomes and comparisons were prespecified and how they were ordered. Those details are not reported in the registry record. The primary result remains distinct from the secondary findings, but the record does not describe any broader testing hierarchy.

Missing-data handling is stated for the primary endpoint: the analysis used last observation carried forward, using the last observed post-baseline double-blind value. The registry does not report how many measurements were missing, when they were missing, why they were missing, or whether missingness differed between groups. It also does not report sensitivity analyses testing alternative assumptions. Carrying a value forward is one way to form analysis values, but its reliability depends on whether the carried observation reasonably represents the later unobserved outcome.

The primary analysis population required receipt of at least one dose and at least one post-randomization efficacy measurement. This definition is stated, but the registry does not report the full analysis population’s relationship to all randomized participants or reasons for any differences. The secondary outcome analysis populations are not described with equivalent detail. No separate intention-to-treat analysis is listed in the record.

These omissions limit how completely the robustness of the estimates can be assessed. They do not invalidate the posted estimates, but they leave uncertainty about the impact of missing observations, analysis-population choices, and multiple testing. The original trial protocol and statistical analysis plan are not reported in the registry record.

15. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: vestibular neuronitis (1.0%), breast cancer (1.0%), gastric cancer (1.0%), contusion (1.0%).

The serious adverse event counts are reported alongside the number at risk in each group. The registry lists 4 affected participants among 104 at risk in the placebo group and 0 among 99 at risk in the teneligliptin group. These are descriptive counts from the posted safety record. They do not, by themselves, establish whether an event was caused by the study treatment or permit a complete comparison of risk.

The record also lists other adverse events affecting 63 participants in the placebo group and 62 in the teneligliptin group, with the respective numbers at risk stated in the safety data. The listed serious-event terms include vestibular neuronitis, breast cancer, gastric cancer, and contusion, each recorded at 1.0%. The registry record does not specify a treatment-group attribution for those terms in the listed summary.

Deaths are not reported in the registry record. Safety counts should be interpreted within the study’s 12-week duration and the participants represented in the safety data. The registry summary does not provide event-level timing, severity detail beyond the serious-event classification, or a causal assessment sufficient to determine treatment attribution.

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

The posted primary estimates show a lower mean change in HbA1c for teneligliptin than for placebo at Week 12, with a negative recalculated contrast and an interval entirely below zero. The unadjusted p-value is <0.001. This describes the statistical comparison in the registry’s defined analysis population and supports a clear difference in the measured endpoint under the stated analysis approach.

That result does not establish how the estimate would change with longer follow-up, in populations other than Japanese patients with type 2 diabetes, or under a different missing-data method. The study assessed a 12-week period. The record does not provide a clinically important difference threshold, so statistical separation cannot alone determine the practical importance of the size of the change.

The result also does not settle questions about outcomes that were not measured. HbA1c and the listed glucose measures are specific continuous outcomes. They are not, by themselves, evidence about long-term complications, quality of life, or other endpoints not reported in the registry. Nor does a small unadjusted p-value express the probability that the treatment effect is true.

Safety findings must be considered separately. The posted serious adverse event counts and other adverse event counts are descriptive, and the record does not provide enough information to assign causality to individual events. The absence of a reported death count is not evidence that no deaths occurred; deaths are not reported in the registry record.

Overall, the record supports an interpretation of the Week 12 statistical estimates, alongside the stated limits in analysis reporting. It does not warrant a broad treatment recommendation or a conclusion about longer-term clinical outcomes.

17. Why This Trial Matters Statistically

This study illustrates how a registry result combines an adjusted primary estimate with summary statistics that can be used to describe uncertainty. The primary analysis is not merely a comparison of observed group changes: it uses ANCOVA, treating treatment as a fixed effect and baseline HbA1c as a covariate. Recognizing that distinction matters when interpreting the least-squares means and their standard errors.

It also illustrates the difference between a prespecified primary outcome and several related secondary measures. The secondary directions align with the primary result, but the record does not report a multiplicity strategy. Statistical consistency across related endpoints is informative context, yet it does not erase the extra uncertainty introduced by multiple testing or by incomplete analysis documentation.

The missing-data approach is consequential to interpretation. Last observation carried forward is explicitly stated for the primary analysis, which makes the analysis rule visible, but the record does not describe the missingness pattern or sensitivity analyses. A clearly named method is not the same as evidence that its assumptions are appropriate for every participant.

Finally, the sample-size figures show how planning changes when the target effect is reduced, while remaining separate from the trial’s original design. The registry does not report the original sample-size justification. Keeping observed results, recalculated comparisons, and hypothetical planning illustrations distinct is essential for sound statistical reading.

18. 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 assessment was at Week 12, and the registry does not report longer-term results. The study population was Japanese patients with type 2 diabetes, so the estimates directly describe that study context; the record does not establish how well they generalize to other populations. The registry does not report baseline characteristics beyond the adjustment for baseline HbA1c in the primary model.

The primary analysis used last observation carried forward. The amount, timing, and reasons for missing data are not reported in the registry record, nor are sensitivity analyses using alternative approaches. The analysis population required both treatment exposure and post-randomization efficacy data, and the record does not explain exclusions or provide a separately reported intention-to-treat analysis.

The registry reports least-squares means and standard errors for the primary endpoint, while the comparison statistics are unadjusted recalculations from posted summary statistics. The record does not give a confidence level for the interval, and no multiplicity adjustment is reported for the secondary outcomes. Secondary outcome analysis populations and missing-data procedures are not described with the same detail as the primary analysis.

The original sample-size rationale, power target, and design assumptions are not reported. Consequently, the planning illustrations based on the observed effect cannot be used to reconstruct the original design. The safety record lists counts and selected serious-event terms, but deaths are not reported and the summary does not establish causal attribution. These limitations constrain interpretation without changing the numerical estimates posted in the record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Monotherapy Study of MP-513 in Patients With Type 2 Diabetes — NCT00998881.
• Registry record last updated 2026-01-02; status last verified 2025-12.
• Results first posted 2014-02-21.
• 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.

22. Record Summary

NCT00998881 is a completed, randomized, quadruple-masked, parallel-group Phase III study comparing oral teneligliptin 20 mg once daily with matching placebo in Japanese patients with type 2 diabetes. The registry records a 12-week administration period, enrollment of 203, a start of 2009-09, and primary completion in 2010-06.

The primary endpoint was change from baseline in HbA1c at Week 12, analyzed using ANCOVA with treatment and baseline HbA1c. The posted group estimates were 0.17 for placebo and -0.62 for teneligliptin; the unadjusted recalculated contrast was -0.79, with an interval from -0.929 to -0.651 and p <0.001. Three secondary glucose outcomes were also listed, with negative estimated contrasts and unadjusted p-values of <0.001.

The primary analysis used last observation carried forward. The record does not report a multiplicity strategy, the original sample-size justification, or deaths. Safety counts are descriptive and do not establish event causality.