Efficacy and Safety Study of MP-513 in Combination With Sulfonylurea in Patients With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of MP-513 in Combination With Sulfonylurea in Patients With Type 2 Diabetes (NCT00974090), a randomized phase 3 study. The primary outcome is Change From Baseline in HbA1c at Week 12.

2. Clinical Question

The clinical question is framed around a laboratory measure of glycemic status rather than a clinical event. HbA1c represents glucose bound to hemoglobin, expressed as a percentage. The registry also identifies fasting plasma glucose and postprandial plasma glucose measures as secondary outcomes. Those outcomes provide related information about glucose measurements at Week 12, but they do not replace the primary comparison.

The record describes a randomized, parallel-group study, so the primary efficacy comparison is between assigned groups. The posted results are estimates from the registry record, not a complete account of every analysis or every outcome that may have been collected. Further details about allocation procedures, group-specific treatment schedules, and the full statistical analysis plan are not reported in the registry record.

3. Trial Design

The registry identifies NCT00974090 as a completed Phase III, randomized, quadruple-masked, parallel-group trial sponsored by Tanabe Pharma Corporation. The stated study population was Japanese patients with type 2 diabetes mellitus. The enrollment entry is 194. The record gives a start date of 2009-09 and a primary completion date of 2011-03.

The two intervention labels are Placebo / Teneli + SU and Teneli / Teneli + SU. Teneli refers to teneligliptin, and SU refers to sulfonylurea. The brief description says the study evaluated safety and efficacy during 12 weeks of administration and with extension treatment for up to 52 weeks. The arm descriptions themselves are blank, so additional detail about the treatment sequences is not reported in the registry record.

Randomization means treatment groups are formed through an assignment process intended to reduce systematic differences at baseline. Masking is intended to limit the influence of treatment knowledge on conduct or assessment. The record labels the masking quadruple, but does not define which parties were masked or describe the masking procedures. The parallel-group designation indicates that the study compared groups rather than describing a crossover design.

The posted primary endpoint is change from baseline in HbA1c at Week 12. The efficacy population is described as the full analysis set, consisting of patients who received at least one dose and had at least one efficacy datum after randomization. The registry reports that missing postbaseline values were handled using last observation carried forward. The exact numbers analyzed for the primary outcome are reported as 98.0 and 96.0 in the group summaries, while the full eligibility and handling of any other missing observations are not elaborated.

The registry lists three secondary glucose outcomes at Week 12: fasting plasma glucose, postprandial plasma glucose area under the curve from 0 to 2 h, and 2-hour postprandial plasma glucose. It also lists safety results extending through Week 52. The registry record does not report the original sample-size justification, interim analyses, detailed allocation procedures, or a complete protocol description.

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.

Period 1: Double Blind Period

Reasons for not completing this period:

Period 2: Open-label Period

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 at Week 0 and Week 12.

The primary endpoint is change from baseline in HbA1c at Week 12, expressed as a percentage of HbA1c. HbA1c reflects glucose bound to hemoglobin. Because it captures glucose exposure over time rather than a single measurement at one moment, it is commonly used as a continuous measure of glycemic status in clinical studies. That general role explains why it can serve as an efficacy endpoint; it does not by itself establish the importance of a particular change for an individual patient.

The registry reports least-squares means rather than simple raw group means. The stated estimates come from an analysis of covariance model with treatment as a fixed effect and baseline HbA1c as a covariate. This adjustment accounts statistically for the baseline HbA1c measure when estimating the group means. The registry identifies the dispersion beside each group estimate as a standard error, which describes the sampling precision of the estimated mean under the model. It is not the same quantity as the variation among individual patients.

The endpoint compares change from baseline at Week 12. A negative change indicates a decrease relative to baseline, while a positive change indicates an increase. The posted group estimates are 0.29 for Placebo / Teneli + SU and -0.71 for Teneli / Teneli + SU; the posted mean difference is -1.0. These are model-based registry estimates for the defined analysis population and the stated missing-data approach. The registry does not report a clinical threshold for interpreting the magnitude of a change.

In general, a continuous endpoint preserves information across the range of measured values rather than reducing results to a binary outcome. The relevance of a continuous measure still depends on the endpoint definition, follow-up, analysis method, and context. The Week 12 HbA1c outcome is a specific short-term endpoint and should not be read as a complete measure of all outcomes during the extension period.

7. Results Posted in the Registry

• Teneli / Teneli + SU: mean -0.71 versus 0.29 on control; difference -1.00 (95% CI -1.17 to -0.83), standardized effect d = -1.69; 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:
  • Teneli / Teneli + SU: mean -17.30 versus 9.80 on control; difference -27.10 (95% CI -33.20 to -21.00), standardized effect d = -1.25; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Teneli / Teneli + SU 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:
  • Teneli / Teneli + SU: mean -65.54 versus 15.51 on control; difference -81.06 (95% CI -97.89 to -64.23), standardized effect d = -1.39; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Teneli / Teneli + SU 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:
  • Teneli / Teneli + SU: mean -43.10 versus 6.00 on control; difference -49.10 (95% CI -61.30 to -36.90), standardized effect d = -1.16; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Teneli / Teneli + SU than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The three secondary outcomes cover fasting glucose and postprandial glucose, complementing the primary HbA1c measure with related glucose assessments. Across the posted secondary comparisons, the estimated differences favor a more negative change in the Teneli / Teneli + SU group, and each reported unadjusted p-value is <0.001. The overall direction is therefore consistent with the primary endpoint’s direction in this registry record.

These are related measures, not independent confirmations of the primary result. They assess glucose at different conditions or summarize post-meal measurements over time, while the primary outcome is HbA1c change. Agreement across related outcomes can make the pattern easier to interpret, but shared participants, measurements, and biological relationships mean the results may not provide wholly separate evidence.

The registry lists the secondary outcome definitions and estimates but does not list separate reported analysis records or a multiplicity strategy. When several outcomes are tested, the chance of at least one small p-value can increase. Without a prespecified hierarchy or statistical adjustment, unadjusted secondary p-values should be treated as supportive and exploratory rather than as equivalent to a separately confirmed primary finding.

The secondary endpoints are all reported at Week 12. They therefore add information about the short-term measurement pattern but do not establish that the same differences continued through the extension period. They also do not supply patient-level information, subgroup effects, or a clinical threshold for interpreting the magnitude of each change. Their role is to provide context around the main endpoint, with the primary outcome retaining the clearest confirmatory status in the posted results.

Interpretation should account for how the outcomes were analyzed. The secondary results are continuous least-squares mean estimates, and the registry gives standard errors for the group values. The record does not describe whether the same missing-data approach, covariate adjustment, or model diagnostics applied to every secondary outcome. Those details are not reported in the registry record, so the secondary findings should be read within the limits of the methods stated for the outcome entries.

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

Statistical methods determine how a study’s measurements are converted into estimates and how much uncertainty accompanies those estimates. The registry gives some important details for the primary endpoint: a least-squares mean change, an analysis of covariance model, baseline HbA1c as a covariate, and last observation carried forward for missing postbaseline measurements. It does not provide a complete statistical analysis plan, so methods beyond those stated should not be inferred.

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of a group mean. It is adjusted for variables included in the statistical model. In this trial’s primary analysis, treatment is the fixed effect and baseline HbA1c is the covariate. The reported values therefore reflect the fitted model’s estimates after accounting for baseline HbA1c, rather than being presented as unadjusted averages of all observed changes. The registry does not provide the full model output or enough detail to reproduce the analysis independently.

Adjustment can be useful when baseline values are related to follow-up measurements. The model uses the baseline covariate to account for that relationship while estimating the treatment-group comparison. The adjustment does not guarantee that all possible imbalances or sources of bias have been addressed. Its interpretation depends on the model being appropriate for the data and on the assumptions used in fitting it. Further diagnostics and model specifications are not reported in the registry record.

What does the standard error describe?

The standard error describes how precisely a model-based estimate is estimated from the data under the model. Smaller standard errors generally indicate less sampling variability in the estimate. A standard error is not the same as the standard deviation of patient-level values: the standard deviation describes spread among observations, whereas the standard error describes uncertainty in an estimated statistic. The registry labels the primary group dispersion as standard error and reports 0.06 for each group.

Confidence intervals use an estimate and its uncertainty to give a range of values compatible with the data under a specified procedure. Their width depends on the estimate’s standard error and the interval method. An interval that excludes zero for a difference is consistent with evidence against a zero-difference null hypothesis at the corresponding confidence level, subject to the method and assumptions. It is not a probability distribution over the effect and does not describe the range of individual patient outcomes.

Why use a mean difference?

For a continuous endpoint, a mean difference summarizes the contrast between estimated group means in the original measurement units. Here, the primary contrast is expressed in percentage points of HbA1c. Preserving the endpoint’s units helps readers understand what quantity is being compared. Standardized effect measures may also be used for planning or comparison across scales, but they do not replace the original-unit estimate. The posted results include a pooled standard deviation approximation and a standardized effect for planning purposes; these are derived summaries rather than additional clinical endpoints.

The registry’s unadjusted p-value for the primary comparison is <0.001. A p-value quantifies how unusual data at least as inconsistent with the null model would be if the null model and test assumptions held. It is not the probability that the null model is true, nor a measure of the clinical importance of the estimate. The p-value should be interpreted alongside the estimate and interval. The registry does not report an adjustment for multiple comparisons.

How does randomization fit into interpretation?

Random assignment is intended to make groups comparable on average with respect to both observed and unobserved baseline characteristics. It supports a causal interpretation when the assignment process is properly implemented and other trial conditions are satisfied. The registry identifies the trial as randomized, but further details about sequence generation, concealment, and implementation are not reported in the registry record. Randomization alone does not resolve issues related to missing outcome data, deviations from assigned treatment, or incomplete reporting.

Masking can reduce the influence of expectations on trial conduct, outcome assessment, and participant reporting. The registry calls the study quadruple-masked, but does not state which roles were masked or how masking was maintained. The label is relevant to design interpretation, but it is not a substitute for procedural details.

What does last observation carried forward assume?

Last observation carried forward fills a missing later measurement with the last available postbaseline measurement. This creates a complete analysis dataset under a specific assumption: the carried-forward value is treated as an acceptable stand-in for the unobserved value at the target time. In general, that assumption may be questionable if outcomes would have changed after the last observed measurement, or if missingness is related to the outcome. The method can understate uncertainty because it treats imputed values as if they were observed. The registry states that this approach was used, but does not report sensitivity analyses comparing it with alternative missing-data methods.

The stated analysis population includes patients who received at least one dose and had at least one efficacy datum after randomization. This differs from an intention-to-treat definition that necessarily includes every randomized participant regardless of post-randomization data availability. The registry’s description should guide interpretation; the record does not provide a fuller accounting of exclusions or missing measurements by group.

Why does over-dispersion matter in other kinds of outcomes?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if a model assumes less variability than the data contain, leading to overly narrow intervals or overly optimistic tests. The primary endpoint is continuous and reported with a standard error from an ANCOVA model, so no over-dispersion assessment is described in the registry record. This concept is relevant generally, but there is no basis in the registry record to say that over-dispersion occurred in this trial.

The planning illustration uses a normal approximation, equal allocation between two groups, and a two-sided significance level of 0.05. These are planning assumptions for illustrative calculations, not evidence of the trial’s original design process. The registry does not report the original sample-size justification or the assumptions used by the trial designers. The planning estimates are based on fractions of the observed effect and are not a substitute for a prospective design calculation based on a clinically justified target effect and an appropriate variance estimate.

11. Confidence Intervals and Precision

The primary comparison is reported as -1.0, with a confidence interval whose lower endpoint is -1.166 and whose upper endpoint is -0.834 in the registry. The interval lies entirely below zero. Because the upper endpoint has more than three decimal places, it is not reproduced numerically; the main point is that the reported interval excludes zero. The registry also reports a standard error of 0.06 for each primary group least-squares mean.

In general, a confidence interval expresses the uncertainty of an estimated effect under a specified statistical procedure. Its width reflects the data and method used; a narrower interval indicates greater precision about the average difference, while a wider interval indicates more uncertainty. An interval does not capture every possible source of uncertainty, such as errors in measurement, limitations in the study population, or departures from the model assumptions.

The interval’s exclusion of zero is consistent with the reported unadjusted p-value of <0.001. Those statistics address the compatibility of the data with a zero-difference model, under the analysis assumptions. They do not establish that the estimated difference is important to patients, and they do not show the range of changes experienced by individuals. The registry does not report a threshold for a clinically meaningful HbA1c change.

The standard errors shown beside the least-squares means are not measures of individual variability. The record does not provide patient-level distributions in this discussion of the outcome results, and the posted interval should not be used to infer that individual responses were uniform. Precision applies to the estimated group contrast, not to the prediction of a particular patient’s outcome.

The registry’s reported confidence interval and p-value relate to the specified primary analysis. They do not automatically account for testing several endpoints. No multiplicity adjustment is reported. The interval also depends on the chosen analysis population and the last-observation-carried-forward procedure; the record does not report alternative missing-data analyses that could show how robust the estimate is to other assumptions.

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 illustrative calculations based on the observed effect and are not the trial’s original design justification. The registry record does not report the original sample-size assumptions. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect targeted in each row is a stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were present. The 90% power column gives the corresponding planning quantity for a 90% chance. Higher target power generally requires more participants when the other assumptions are unchanged. This is not observed power; it is a prospective-style illustration calculated from the observed effect.

For example, the primary endpoint planning illustration lists 6 participants per arm for 80% power and 8 participants per arm for 90% power when targeting 100% of the observed effect. When the target is 75% of the observed effect, the corresponding figures are 10 and 14 participants per arm. For 50% of the observed effect, they are 22 and 30 participants per arm. These are planning examples, not estimates of how many participants the trial actually needed or a justification for the trial’s enrollment.

Smaller effects are harder to distinguish from random variation, so the illustration requires more participants per arm as the target effect becomes smaller. Such calculations are sensitive to assumptions about the effect size, variability, significance level, allocation, and analysis. Since the planning values use the observed effect, they should not be treated as independent evidence that the study was adequately designed. The original design rationale and any allowance for missing data or attrition are 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 = -1.000; pooled standard deviation σ = 0.591.
2. n = 2 × (1.96 + 0.842)² × 0.591² / -1.000² = 5.5, rounded up to 6 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                      # observed difference in means
sigma <- 0.590963196823626                     # 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(974090)
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 = 6 (80% power), 8 (90% power)
 75% of observed effect: n per arm = 10 (80% power), 14 (90% power)
 50% of observed effect: n per arm = 22 (80% power), 30 (90% power)
power.t.test: 6.6 
Simulated power at n = 6 per arm: 0.755 (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

Multiplicity arises when several statistical hypotheses are tested within a study. Even if every null hypothesis were true, conducting many tests can increase the chance that at least one result appears statistically notable by chance. Common approaches include adjusting the significance threshold, controlling a family-wise error rate, or specifying a testing hierarchy in advance. These are general methods; the registry record does not say that any particular approach was used in this trial.

The registry posts one primary endpoint and three secondary glucose endpoints. The primary comparison has an unadjusted p-value of <0.001, and each secondary comparison also has an unadjusted p-value of <0.001. The record does not report whether the primary endpoint was tested within a prespecified hierarchy, whether the secondary outcomes were formally controlled for multiplicity, or whether other analyses were conducted. The secondary findings should therefore be interpreted with less confirmatory weight than the primary result.

The registry describes the primary analysis population as patients who received at least one dose and had at least one efficacy datum after randomization. This definition is important because it identifies who contributed to the efficacy analysis, but it does not give a complete flow of randomized participants, exclusions, or missing data by group. The record states that last observation carried forward was used for missing postbaseline values. It does not report sensitivity analyses under other missing-data assumptions or explain how missingness may have differed between groups.

Last observation carried forward can be easy to describe, but it rests on assumptions about what the unobserved later measurement would have been. In general, if the outcome changes after the last observation or missingness is related to the outcome, carrying a value forward can distort the estimated mean and its uncertainty. Alternative approaches can assess robustness, but such analyses are not reported in the registry record.

The record identifies the study as randomized and quadruple-masked, but further information about randomization procedures, masking roles, allocation concealment, protocol deviations, and analysis-plan specifications is not reported in the registry record. Interim analyses and stopping rules are also not reported in the registry record. These absences limit assessment of the statistical safeguards around the result; they do not show that such procedures were or were not used.

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: gastric cancer (2.1%), large intestine carcinoma (2.1%), maculopathy (1.1%), cataract (1.1%), retinal vein occlusion (1.1%).

The safety entries report serious adverse events by group and time window. Through Week 12, the record lists 2 serious adverse events among 98 at risk in the Placebo / Teneli + SU group and 0 among 96 at risk in the Teneli / Teneli + SU group. For the later period, the Placebo / Teneli + SU entry is labeled Week 12 to Week 52 and lists 2 among 95 at risk; the Teneli / Teneli + SU entry is labeled through Week 52 and lists 7 among 96 at risk.

These entries should be read using their stated time windows and denominators. The group labels and periods are not identical across the later entries, so the counts should not be treated as a simple like-for-like comparison of cumulative risk. The registry does not provide a statistical comparison of these serious-event counts. It also does not report deaths in the listed safety entries.

The record separately lists other adverse events: 60 among 98 and 62 among 96 through Week 12, and 89 among 95 and 89 among 96 in the later entries. These counts are distinct from serious adverse events. Serious-event terms listed in the record include gastric cancer, large intestine carcinoma, maculopathy, cataract, retinal vein occlusion, and colonic polyp. The event entries are descriptive; they do not by themselves establish that a treatment caused an event or provide a complete assessment of comparative safety.

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

The primary result is an adjusted average comparison of change in HbA1c at Week 12 for the defined analysis population. The estimate is -1.0 percentage points for Teneli / Teneli + SU relative to Placebo / Teneli + SU, with group changes of -0.71 and 0.29. The confidence interval lies below zero, and the registry reports an unadjusted p-value of <0.001. These findings describe the posted analysis, not an individual patient’s likely response.

The result does not establish the clinical importance of the difference. The registry record does not report a threshold for a meaningful change, patient-reported outcomes, or a comparison of clinical events. Statistical evidence about a mean difference is not the same as evidence about a particular person’s experience, and the group average does not reveal the distribution of responses.

The endpoint is measured at Week 12. Although the study description includes extension treatment for up to 52 weeks and safety entries through Week 52, the posted primary efficacy comparison is not a Week 52 estimate. The record does not report a corresponding primary endpoint comparison for the extension period, so persistence of the Week 12 difference cannot be concluded from this result.

The findings also do not establish generalizability beyond the study population described in the registry. The official title identifies Japanese patients with type 2 diabetes mellitus, and the record does not provide subgroup estimates or information about other populations. The result should be interpreted in the context of the randomized, masked trial design, the stated analysis population, and the stated missing-data method.

Safety counts do not transform the efficacy estimate into a complete benefit-harm assessment. Serious adverse events are reported descriptively, with different later-period labels and no comparative statistical analysis. The registry record does not report deaths in the safety entries. A complete interpretation would require attention to the full outcome set, follow-up, missing data, treatment exposure, and analysis procedures, several of which are not reported in the registry record.

In general, trial results are most informative when the endpoint, analysis, uncertainty, and population are considered together. The posted estimates provide evidence about a specific Week 12 average comparison under the registry’s stated method. They do not provide medical advice, guarantee an outcome, or answer every question about longer-term effects or safety.

17. Why This Trial Matters Statistically

This trial is statistically informative because it places a continuous primary endpoint alongside related glucose outcomes and describes the main model used for the primary comparison. The least-squares mean approach adjusts for baseline HbA1c, and the registry reports both a treatment contrast and a confidence interval. Together, those quantities allow interpretation of the estimated average difference and its precision rather than relying only on a significance test.

The record also illustrates why endpoint hierarchy matters. A primary outcome gives a study’s principal confirmatory question a defined place, while secondary outcomes can add context. Here, the secondary glucose measures show a direction aligned with the primary estimate, but their unadjusted tests cannot be treated as independent confirmations when the multiplicity plan is not reported. Clear reporting of endpoint hierarchy and adjustment methods is essential for judging the strength of a body of trial evidence.

Missing-data handling is another key statistical feature. The registry states that last observation carried forward was used for the primary endpoint. Naming the method helps readers understand how missing postbaseline values entered the analysis, while the absence of sensitivity analyses leaves uncertainty about robustness to alternative assumptions. This is a reminder that a result depends not only on the fitted model but also on decisions about which observations contribute and how missing values are treated.

Finally, the safety entries show the importance of respecting follow-up windows and denominators. The later serious-event entries use different period labels, and the record gives no formal comparative analysis. Reading counts without that context could overstate what the data establish. A careful statistical reading separates descriptive safety summaries from efficacy estimates and distinguishes what is reported from what remains unreported.

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 registry record gives useful details about the primary endpoint, analysis model, population, and missing-data method, but leaves important design and analysis information unreported. The original sample-size justification, analysis-plan details, interim analyses, and multiplicity strategy are not reported in the registry record. The planning calculations are based on the observed effect and should not be mistaken for the trial’s prospective design rationale.

The efficacy analysis uses a population defined by receiving at least one dose and having at least one efficacy datum after randomization. The registry does not provide a full participant flow or a detailed account of missing observations and exclusions by group. Last observation carried forward is stated as the missing-data method, but alternative analyses are not reported. This limits assessment of how sensitive the primary result may be to missing-data assumptions.

The primary result is a Week 12 comparison, while the study description includes extension treatment up to 52 weeks. The posted primary efficacy result therefore does not answer whether the same comparison continued over the longer period. The safety entries span different periods and later group labels are not identical, limiting direct comparisons of the reported serious-event counts. Deaths are not reported in the safety entries.

The registry describes the study as randomized and quadruple-masked, but procedural details about allocation, concealment, and masking roles are not reported. The arm descriptions are also blank. Thus, the treatment labels and broad design can be described, but more specific aspects of treatment sequencing and conduct cannot be reconstructed from the registry record.

The reported secondary outcomes are related glucose measures with unadjusted comparisons. Without a reported multiplicity strategy, they should not carry the same confirmatory weight as the primary outcome. The record also does not report a clinical threshold for interpreting the size of the HbA1c difference, subgroup analyses, or a complete set of sensitivity analyses. These limitations restrict conclusions about clinical importance, generalizability, and robustness.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of MP-513 in Combination With Sulfonylurea in Patients With Type 2 Diabetes — NCT00974090.
• Registry record last updated 2026-01-05; status last verified 2025-12.
• Results first posted 2014-05-08.
• 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

NCT00974090 is a completed Phase III randomized, quadruple-masked, parallel-group study sponsored by Tanabe Pharma Corporation. The registry describes Japanese patients with type 2 diabetes and enrollment of 194. The record lists a start date of 2009-09 and primary completion at 2011-03.

The primary endpoint is change from baseline in HbA1c at Week 12. Least-squares mean changes were 0.29 for Placebo / Teneli + SU and -0.71 for Teneli / Teneli + SU; the mean difference was -1.0, with an unadjusted p-value of <0.001. The stated analysis used ANCOVA with baseline HbA1c as a covariate and last observation carried forward for missing postbaseline values.

Three secondary glucose outcomes were posted, with unadjusted comparisons. Safety entries include serious and other adverse events through Week 12 and later periods through Week 52, with differing period labels. The registry record does not report the original sample-size justification, a multiplicity strategy, interim analyses, or deaths in the listed safety entries.