Bioequivalence Study of Saxagliptin and Glucophage Combination Formulations in Healthy Subjects (A): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bioequivalence Study of Saxagliptin and Glucophage Combination Formulations in Healthy Subjects (A) (NCT00899470), a randomized phase 1 study. The primary outcome is Saxagliptin Mean Maximum Observed Plasma Concentration (Cmax).

2. Clinical Question

3. Trial Design

This was a Phase 1, randomized, unmasked crossover study sponsored by AstraZeneca. The registry reports that 24 participants were enrolled. The study is described as involving healthy subjects, and the primary pharmacokinetic population is participants who received study drug. The trial status is completed; the recorded start was 2009-06 and primary completion was 2009-08.

In a crossover design, participants receive more than one study condition in a planned sequence, so comparisons can be made within the same participant. The registry lists sequences that include both formulations in fasted and fed conditions. This design can account for stable differences between participants when the analysis uses the within-participant structure appropriately. The sequence schedule in the record identifies treatment order, but details such as washout periods and any period or sequence effects are not reported in the registry record.

The intervention contrast was between the fixed-dose combination of saxagliptin and metformin immediate release and separate saxagliptin and metformin immediate-release tablets taken together. Each was assessed in a fasted condition and a fed condition. The primary measure was saxagliptin Cmax, or maximum observed plasma concentration. The registry also lists pharmacokinetic outcomes for BMS-510849 and safety outcomes. The precise procedures for establishing fed and fasted status, dosing administration, and handling departures from the planned sequence are not reported in the registry record.

Randomization helps limit systematic differences in treatment order, but the record does not report how the random sequence was generated or concealed. Masking is recorded as none. The original protocol's statistical plan, sample-size justification, interim analyses, and planned handling of missing observations are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 85 participants were enrolled and 24 were treated on study. 61 participants discontinued before randomization and treatment due to: no longer meeting study criteria (n=36), withdraw of consent (n=3), study was full (n=15), participant did not call for results (n=1), completed alternate status (n=5), or did not show for check-up (n=1)

First Therapy

First Washout Period

Second Therapy

Second Washout

Analysis population for the primary outcome, as defined in the registry: PK data set, all participants who received study drug

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 Saxagliptin Mean Maximum Observed Plasma Concentration (Cmax), measured over Day 1: 0 hr, 0.25 hr, 0.5 hr, 0.75 hr, 1 hr, 1.5 hr, 2 hr, 3 hr, 4 hr, 6 hr, 8 hr, 12 hr, 18 hr, Day 2: 0 hr, 12 hr, Day 3: 0 hr.

The primary endpoint is the mean maximum observed plasma concentration, or Cmax, of saxagliptin after a single dose of 2.5 mg. Concentration was assessed at a series of scheduled time points spanning Day 1 through Day 3. The endpoint represents the highest observed plasma concentration during the sampling schedule, rather than total exposure over time. The registry reports the unit as ng/mL and describes the summary as a mean with standard deviation.

Cmax is a pharmacokinetic measure: it describes the peak concentration recorded after dosing. In a bioequivalence study, comparing this measure between formulations helps assess whether the formulations produce similar peak exposure under the studied conditions. It is considered alongside other pharmacokinetic measures, including area under the concentration-time curve, which reflects exposure across time. The registry's stated objective was to demonstrate bioequivalence between the fixed-dose combination and the separately co-administered tablets in both fasted and fed states.

The endpoint is not itself a measure of clinical benefit or harm. It describes drug concentration in the studied participants, and its interpretation depends on the planned bioequivalence criteria and analysis. The registry record does not report the equivalence margins or a detailed rationale for selecting Cmax as the primary endpoint. The sponsor's reported analysis expresses the comparison as a geometric mean ratio, while the posted group summaries and simple recalculations use arithmetic means and mean differences; these are different statistical summaries.

7. Results Posted in the Registry

• Saxagliptin/Metformin FDC (Fasted): mean 8.61 versus 8.57 on control; difference 0.04 (95% CI -1.33 to 1.41), standardized effect d = 0.02; z-test p = 0.954.
• Coadministration of Saxagliptin and Metformin IR (Fed): mean 11.36 versus 8.57 on control; difference 2.79 (95% CI 1.25 to 4.33), standardized effect d = 1.02; z-test p = <0.001.
• Saxagliptin/Metformin FDC (Fed): mean 11.51 versus 8.57 on control; difference 2.94 (95% CI 1.11 to 4.77), standardized effect d = 0.91; z-test p = 0.002.

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.

BMS-510849 Mean Cmax

• 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 deviations.
• Result:
  • Saxagliptin/Metformin FDC (Fasted): mean 16.10 versus 16.32 on control; difference -0.22 (95% CI -3.07 to 2.63), standardized effect d = -0.04; z-test p = 0.880.
  • Coadministration of Saxagliptin and Metformin IR (Fed): mean 18.40 versus 16.32 on control; difference 2.08 (95% CI -0.55 to 4.71), standardized effect d = 0.45; z-test p = 0.121.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Saxagliptin/Metformin FDC (Fasted) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Coadministration of Saxagliptin and Metformin IR (Fed) and the control. The interval gives the range of effects that remain compatible with the data.

BMS-510849 Mean AUC (0-T)

• 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 deviations.
• Result:
  • Saxagliptin/Metformin FDC (Fasted): mean 113.87 versus 112.35 on control; difference 1.52 (95% CI -11.04 to 14.08), standardized effect d = 0.07; z-test p = 0.812.
  • Coadministration of Saxagliptin and Metformin IR (Fed): mean 120.31 versus 112.35 on control; difference 7.96 (95% CI -4.16 to 20.08), standardized effect d = 0.37; z-test p = 0.198.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Saxagliptin/Metformin FDC (Fasted) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Coadministration of Saxagliptin and Metformin IR (Fed) and the control. The interval gives the range of effects that remain compatible with the data.

BMS-510849 Mean AUC (0-INF)

• 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 deviations.
• Result:
  • Saxagliptin/Metformin FDC (Fasted): mean 122.74 versus 120.72 on control; difference 2.02 (95% CI -10.68 to 14.72), standardized effect d = 0.09; z-test p = 0.755.
  • Coadministration of Saxagliptin and Metformin IR (Fed): mean 129.02 versus 120.72 on control; difference 8.30 (95% CI -3.84 to 20.44), standardized effect d = 0.39; z-test p = 0.180.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Saxagliptin/Metformin FDC (Fasted) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Coadministration of Saxagliptin and Metformin IR (Fed) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary pharmacokinetic summaries generally show higher reported means in the fed conditions than in the fasted conditions, while the fixed-dose combination and separate co-administration summaries are relatively close within the same food condition for the measures reported. This broad pattern is consistent with the primary endpoint's descriptive contrast: the formulation summaries are close within the fasted condition, and fed-condition Cmax summaries are higher than fasted-condition summaries. These observations describe the posted values; they do not establish a causal food effect or demonstrate bioequivalence across all endpoints.

Secondary outcomes include BMS-510849 Cmax and area-under-the-curve measures, along with additional pharmacokinetic and safety outcomes. The registry lists outcomes for mean AUC from zero to the last measured time, mean AUC from zero to infinity, half-life, and time to maximum concentration. It also lists adverse events, laboratory abnormalities, electrocardiogram abnormalities, and vital-sign abnormalities. Not all listed outcomes have detailed results in the record; where results are absent, they are not reported in the registry record.

Secondary analyses are less persuasive as confirmatory evidence when many outcomes or comparisons are examined without a reported adjustment or prespecified hierarchy. A nominal unadjusted result can arise by chance among repeated tests, and a non-significant result does not establish that there is no difference. The registry record does not report how multiplicity was handled or which secondary endpoints, if any, were designated as confirmatory. The secondary results therefore add descriptive context to the primary pharmacokinetic comparison but cannot independently settle the bioequivalence question.

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

• BMS-510849 Mean Cmax
• BMS-510849 Mean AUC (0-T)
• BMS-510849 Mean AUC (0-INF)
• BMS-510849 Mean T-half and T-max
• Number of Participants With at Least 1 Adverse Event (AE), Death, Serious AE (SAE), or AEs Leading to Discontinuation
• Number of Participants With Laboratory Marked Abnormalities
• Number of Participants With Clinically Relevant Electrocardiogram (ECG) Abnormalities
• Number of Participants With Clinically Relevant Vital Sign Abnormalities

9. Statistical Interpretation

10. Statistical Methods Explained

The record contains two distinct kinds of comparison for the primary endpoint. The sponsor reports geometric mean ratios from its analysis. Separately, the simple recalculations compare posted arithmetic means using mean differences. The latter are unadjusted recalculations from summary statistics, not a reproduction of the sponsor's model. Since this study used a crossover design, comparisons that treat group summaries as independent do not account for the within-participant correlation that may be present. The registry's detailed model specification is not reported in the registry record.

What does a mean difference describe?

A mean difference expresses the amount by which one reported group mean is higher or lower than another, in the endpoint's original units. For Cmax, the unit is ng/mL. The recalculated differences use the fasted co-administration group as the reference for the listed comparisons. A difference near zero indicates that the two arithmetic mean estimates are close in this dataset. It does not by itself establish that two formulations are equivalent: that requires a prespecified acceptable range and an analysis aligned with the study design.

The arithmetic mean is sensitive to the scale and distribution of measurements. Pharmacokinetic analyses commonly use log-transformed values and geometric summaries, but the registry's reported sponsor analysis is identified as a mixed models analysis for the fasted comparison and as a geometric mean ratio for both comparisons. The exact transformation and model terms are not fully reported in the registry record. The sponsor's model-based ratios and the arithmetic mean differences therefore should be read as separate summaries, not as interchangeable versions of one estimate.

Why is the crossover structure important?

In a crossover trial, the same participant can contribute observations under multiple treatments. Those observations are generally related: a participant's values may tend to be relatively high or low across conditions. An analysis that uses the pairing can estimate the treatment contrast while accounting for this within-participant relationship. A calculation based only on separate means and standard deviations cannot recover that relationship. Its interval and p-value may therefore differ from those produced by an appropriate crossover model. The recalculated results are useful as transparent, unadjusted comparisons of posted summaries, but they are not a substitute for the sponsor's analysis.

Randomization of treatment sequence is relevant because treatment order, time, and carryover can affect measurements. The record lists randomized sequences but does not report the randomization procedure, washout details, or how period and sequence effects were handled. Those details matter when judging whether the statistical analysis reflects the design. The sponsor's mixed-model method is named for one reported analysis, but its full specification is not reported in the registry record.

What does a confidence interval communicate?

As a general statistical concept, a confidence interval describes the range of estimates compatible with the data and the method used, under that method's assumptions. A wider interval indicates less precision than a narrower one. An interval that includes zero for a mean difference does not demonstrate equality; it indicates that the data and method do not clearly distinguish the difference from zero at the interval's confidence level. For equivalence questions, interpretation instead depends on whether the interval falls within prespecified equivalence limits. Those limits are not reported in the registry record for this trial.

The sponsor gives 90% confidence intervals for geometric mean ratios. The simple recalculations also provide intervals, but the confidence level for those calculations is not stated in the record. The two interval sets should not be compared as though they necessarily came from the same model or assumptions. The sponsor's intervals are associated with the reported sponsor analysis; the recalculated intervals derive from the posted summary statistics.

How should p-values be read?

A p-value describes how unusual data at least as discrepant as those observed would be under a specified null model, assuming that model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or clinical importance of a difference. The recalculated p-values are unadjusted. They are not reported sponsor p-values, and the registry does not state that they were used in the trial's bioequivalence decision.

For a bioequivalence objective, a conventional test of no difference is not the same as a test of equivalence. Failure to find a statistically detectable difference does not prove that the formulations are sufficiently close. The decision requires an equivalence framework, including acceptable limits and an analysis plan. Those details are not reported in the registry record. Accordingly, the sponsor's ratio estimates and intervals are the relevant posted evidence for the stated objective, while still requiring the missing criteria for full interpretation.

What do the other statistical summaries add?

The reported group standard deviations describe variation among the measured values within each treatment condition. A standard deviation is not the uncertainty of the mean; it reflects dispersion of participant measurements around their group mean. The standard error, where used in the recalculations, describes the estimated sampling variability of a mean under the calculation's assumptions. In a crossover design, the standard error for a paired contrast depends on the within-participant covariance, which is not available from separate group means and standard deviations alone.

Over-dispersion is a general concern when observed variability is greater than a statistical model assumes. A model that understates variability can yield intervals that are too narrow and tests that are too optimistic; a model that represents variability appropriately gives more credible uncertainty estimates. The registry does not report diagnostic checks or model-fit assessments, so no conclusion about over-dispersion can be drawn for this analysis.

The registry lists 17 outcome measures and 12 analyses, while the posted results include additional pharmacokinetic and safety outcomes. Multiple endpoints and comparisons raise the general possibility of chance findings when each is examined separately. The record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Consequently, unadjusted secondary comparisons are best treated as descriptive and exploratory rather than as a collection of confirmatory tests.

11. Confidence Intervals and Precision

The sponsor's primary analyses report 90% confidence intervals for geometric mean ratios. In the fasted condition, the ratio is 1.011 and its interval runs from 0.940 to 1.088. In the fed condition, the ratio is 0.999 and its interval runs from 0.929 to 1.075. These intervals express uncertainty around the sponsor's ratio estimates under its analysis. The point estimates are near 1, while the intervals include values on either side of 1. Whether the intervals support a formal bioequivalence conclusion depends on the equivalence limits, which are not reported in the registry record.

The recalculated mean differences have their own intervals: 0.04, with an interval from -1.331 to 1.411, for the fasted formulation comparison; 2.79, with an interval from 1.247 to 4.333, for fed co-administration compared with the fasted reference; and 2.94, with an interval from 1.111 to 4.769, for the fed fixed-dose combination compared with the fasted reference. These intervals are not sponsor-reported bioequivalence intervals, and their confidence level is not stated in the registry record. They also do not account for within-participant correlation in the crossover design.

Precision is limited by the small enrollment and the variability in observed Cmax values. A confidence interval is not a guarantee that the true effect lies within its endpoints; as a general concept, it summarizes uncertainty under a specified method and assumptions. Intervals should be interpreted together with the endpoint scale, model, design, and decision criteria. The registry's missing equivalence margins and incomplete model details prevent a complete assessment of precision against the intended bioequivalence standard.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculations. For continuous outcomes such as these pharmacokinetic measures, the figures are participants per arm, not total events. The stated assumptions are 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 trial's own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm under those assumptions for an 80% chance of detecting the selected effect if that effect is the true one and the model assumptions hold. The 90% power column describes the corresponding planning target for a 90% chance. These are design-planning quantities, not observed power. They depend on the effect size and variability used in the illustration, and should not be read as evidence that the completed study had a particular probability of finding a result.

Rows that plan for 75% or 50% of the observed effect use smaller target effects than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. This pattern is visible across the planning figures, although the exact values differ substantially by comparison and endpoint. The observed effect in a small study can be an unstable planning anchor, so these calculations are not a substitute for a prospective design justified using a clinically or scientifically meaningful target.

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 = 0.040; pooled standard deviation σ = 2.424.
2. n = 2 × (1.96 + 0.842)² × 2.424² / 0.040² = 57,639.9, rounded up to 57,640 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 <- 0.0399999999999991                      # observed difference in means
sigma <- 2.42383374017279                     # 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(899470)
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 = 57,640 (80% power), 77,164 (90% power)
 75% of observed effect: n per arm = 102,471 (80% power), 137,180 (90% power)
 50% of observed effect: n per arm = 230,560 (80% power), 308,654 (90% power)
power.t.test: 57640.9 
Simulated power at n = 57,640 per arm: 0.802 (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 own primary analysis is reported as a geometric mean ratio of test versus reference. It gives a fasted ratio of 1.011 with a 90% confidence interval from 0.940 to 1.088, and a fed ratio of 0.999 with a 90% confidence interval from 0.929 to 1.075. The fasted comparison is identified as a mixed models analysis; a method is not specified for the fed comparison. The registry classifies the analyses as noninferiority or equivalence analyses.

The separate recalculations compare arithmetic means and express results as mean differences with unadjusted p-values. They are simple calculations from posted summary statistics and do not reproduce the sponsor's model or take account of the crossover pairing. Their results therefore should not be used to override or reinterpret the sponsor's analysis. There is no discrepancy flagged between the reported outcomes and the recalculations, but the two approaches still answer different statistical questions and use different scales.

The sponsor's ratios are the relevant posted analyses for the stated bioequivalence objective. However, the equivalence margins, detailed model specification, and decision rule are not reported in the registry record. The ratios and intervals can be described, but a formal conclusion against an acceptance standard cannot be independently verified from the registry information alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures, including primary and secondary pharmacokinetic endpoints and several safety outcomes. Multiple comparisons create a general statistical concern: if many hypotheses are tested separately, some may appear statistically notable by chance even when no underlying effect exists. This is why trials may prespecify a hierarchy of endpoints or adjust for multiplicity. The registry record does not report a multiplicity strategy, an endpoint hierarchy, or whether any adjustment was applied to secondary comparisons.

The primary objective is described as demonstrating bioequivalence, and the sponsor analyses are classified as noninferiority or equivalence analyses. Yet the equivalence margins, full decision rule, and complete statistical analysis plan are not reported in the registry record. Those details are central to interpreting whether a ratio interval meets the intended criterion. The reported point estimates and intervals are informative descriptions, but cannot replace the missing prespecified thresholds.

The record identifies the primary pharmacokinetic population as participants who received study drug. The exact analysis population for each sponsor comparison, participant flow, exclusions, and reasons for missing data are not reported in the registry record. Nor are the methods for handling missing concentration measurements or incomplete sampling described. In pharmacokinetic analyses, missing observations can affect estimated peak concentration or exposure, depending on when and why measurements are absent. Without these details, the completeness and robustness of the analyses cannot be fully assessed.

Because this was a crossover study, relevant statistical details include treatment period, sequence, carryover, and participant effects. The registry reports randomization and treatment sequences, but the model terms and diagnostic checks are not reported in the registry record. Interim analyses and the original sample-size justification are also not reported. These omissions limit assessment of whether the analyses followed the planned design and how sensitive the results are to assumptions.

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 4% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events among 24 participants in each of the four treatment-condition groups. This means no serious adverse event was recorded in those group summaries during the reported study experience. The registry also lists other adverse events affecting 6 participants with fasted co-administration, 3 with the fasted fixed-dose combination, 4 with fed co-administration, and 1 with the fed fixed-dose combination. These are participant counts, not event rates calculated for a longer-term exposure period.

Death counts are not reported in the registry record. The serious adverse event summaries should be read in light of the small study and its pharmacokinetic focus. The registry record does not provide enough detail to characterize event timing, recurrence, severity beyond the serious-event classification, or a causal relationship to treatment. These counts describe the posted safety data and do not establish comparative safety.

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

The results describe a randomized crossover comparison of a fixed-dose saxagliptin/metformin immediate-release tablet with separate saxagliptin and metformin immediate-release tablets taken together, in healthy subjects under fasted and fed conditions. The primary endpoint was saxagliptin Cmax. Sponsor-reported geometric mean ratios were 1.011 in the fasted comparison and 0.999 in the fed comparison, with 90% confidence intervals reported for both.

These estimates can be viewed as evidence about the relative pharmacokinetic measurements observed under the study conditions. They are not measures of symptom change, disease control, or clinical outcomes. The record does not report the equivalence margins needed to determine whether the sponsor's intervals satisfy its intended bioequivalence criterion. The arithmetic-mean recalculations are not substitutes for that sponsor analysis and do not reflect the paired crossover structure.

The study does not establish long-term effects, outcomes in people with Type 2 Diabetes Mellitus, or how the formulations compare in populations beyond the healthy subjects studied. The record describes a single-dose pharmacokinetic assessment, not a trial of long-term clinical effectiveness. No medical recommendation follows from these results.

The safety summaries report no serious adverse events in the treatment-condition groups, alongside counts of other adverse events. These data are limited by the study's size and scope, and death counts are not reported in the registry record. They cannot determine the comparative frequency of uncommon or longer-term harms. Overall, the record provides a narrow comparison of pharmacokinetic measures and should be interpreted within that scope.

18. Why This Trial Matters Statistically

This trial is statistically useful as an example of how a bioequivalence question differs from a conventional test for a difference. The sponsor reports geometric mean ratios and confidence intervals, which align with the stated formulation-comparison objective. The unadjusted recalculations instead compare arithmetic means. A p-value that does not indicate a detectable difference would not, by itself, establish equivalence; equivalence requires prespecified limits and an analysis designed to assess those limits.

The crossover design also highlights the importance of matching analysis to design. Participants receive multiple conditions, so their measurements are not necessarily independent. Calculations from separate group summaries cannot recover within-participant covariance. This makes transparent reporting of the model and treatment of period, sequence, and participant effects important for evaluating precision and validity.

Finally, the registry record illustrates how incomplete reporting can constrain interpretation even when point estimates and intervals are available. The sponsor's ratios are posted, but equivalence margins and detailed model specifications are not. Multiple secondary outcomes are listed without a reported multiplicity strategy. The result is that the descriptive pharmacokinetic pattern can be understood, while a complete independent appraisal of the formal decision criteria remains limited.

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 principal limitation is the small enrollment of 24 healthy subjects. The estimates may be imprecise, and the study is not a basis for characterizing uncommon safety outcomes or long-term use. Its population also limits generalization: the study description identifies healthy subjects, despite Type 2 Diabetes Mellitus being listed as a condition in the registry. The eligibility criteria and participant characteristics are not reported in the registry record.

The record does not report the equivalence margins, full statistical analysis plan, detailed model specification, or original sample-size justification. These omissions prevent an independent check of the sponsor's formal bioequivalence decision. Although the study is a crossover trial, the simple recalculations use separate summary statistics and do not incorporate within-participant correlation. Their intervals and p-values therefore should not be treated as design-matched replacements for the sponsor analysis.

Other relevant details are also not reported in the registry record, including washout duration, treatment-period effects, handling of missing measurements, analysis exclusions, and the multiplicity strategy. The posted secondary outcomes are not all accompanied by detailed results. Death counts are not reported. These reporting gaps, together with the limited population and study scope, constrain the conclusions that can be drawn from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Bioequivalence Study of Saxagliptin and Glucophage Combination Formulations in Healthy Subjects (A) — NCT00899470.
• Registry record last updated 2015-06-01; status last verified 2015-05.
• Results first posted 2011-03-25.
• 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

NCT00899470 is a completed Phase 1 randomized, unmasked crossover study sponsored by AstraZeneca. It enrolled 24 healthy subjects and compared a fixed-dose tablet containing 2.5 mg saxagliptin and 500 mg metformin immediate release with the same medicines taken together, under fasted and fed conditions. The primary outcome was saxagliptin mean Cmax.

The sponsor reported geometric mean ratios of 1.011 in the fasted condition and 0.999 in the fed condition, each with a 90% confidence interval. The registry also posts pharmacokinetic secondary outcomes and adverse-event summaries. Equivalence margins, full analysis details, and the original sample-size justification are not reported in the registry record, limiting independent assessment of the formal bioequivalence conclusion.