Bioequivalence of TF3 and TF2 and Effect of Food on the PK of Tepotinib: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bioequivalence of TF3 and TF2 and Effect of Food on the PK of Tepotinib (NCT03629223), a randomized phase 1 study. The primary outcome is Part A, B and C: Area Under the Plasma Concentration-Time Curve From Time Zero to the Last Quantifiable Concentration (AUC 0-t) of Tepotinib.

2. Clinical Question

3. Trial Design

This was a Phase 1, randomized, open-label study with a crossover design. It was completed, enrolled 66 participants, and had a primary completion date of 2019-01-25. The registry lists healthy subjects as the study population. Because the design was open-label, masking was not used.

The study had three parts, each addressing a distinct pharmacokinetic comparison. Part A compared the TF3 test formulation with the TF2 reference formulation under fasting conditions. Participants received the two formulations in different orders. Part B compared TF2 under fasted and fed conditions, with treatment order varied. Part C made the corresponding fasted-versus-fed comparison for TF3, again with treatment order varied. The registry descriptions specify single oral doses of 500 mg; for TF3, the dose is described as 2 x 250 mg.

A crossover design means that a participant can contribute observations under more than one treatment condition. The treatment conditions are therefore not necessarily independent groups of different people. The registry reports 38 participants for each Part A pharmacokinetic condition, 12 for Part B fasted, 14 for Part B fed, and 12 for each Part C condition. These condition-specific counts should not be added to infer the number of unique participants.

The registry describes a 21-day washout period in some arm descriptions, but full details of the washout and other design procedures are not reported in the registry record. The allocation sequence generation and the statistical model used for the reported comparisons are also 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: Overall 142 participants were screened in this study. Out of which 66 participants were randomized into the study.

Treatment Period 1 (21 Days)

Reasons for not completing this period:

Treatment Period 2 (21 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Pharmacokinetic.(PK) Analysis Set included participants without any relevant protocol deviations with respect to PK and absence of factors likely to affect comparability of PK results, with adequate trial medication compliance, who had valid primary endpoints for both treatments for Part A; and who had at least 3 post-dose concentration measurements for Part B; C.

5. Baseline Characteristics

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

Population: The Safety analysis set included all participants who had received at least 1 dose of planned study drug in the respective parts.

6. Primary Endpoint

The registry lists the primary outcome as Part A, B and C: Area Under the Plasma Concentration-Time Curve From Time Zero to the Last Quantifiable Concentration (AUC 0-t) of Tepotinib, measured over Pre-dose, 0.25, 0.5, 0.75, 1, 1.5, 2, 3, 4, 6, 8, 12, 16, 24, 36, 48, 60, 72, 96, 120, 144 and 168 hours post-dose on Day 1 of each treatment period.

AUC 0-t measures cumulative tepotinib exposure in plasma from dosing until the last sampling time at which the concentration remains at or above the lower limit of quantification. The registry says it was calculated using the mixed log-linear trapezoidal rule. Blood sampling was scheduled at multiple times from pre-dose through 168 hours post-dose on Day 1 of each treatment period.

This endpoint is useful in pharmacokinetic comparisons because it incorporates concentration measurements across time rather than relying on a single concentration. Comparing AUC between formulations can characterize whether total measured exposure is similar, while comparing fed and fasted conditions can characterize the effect of food on exposure. These are pharmacokinetic questions, not direct measures of clinical benefit.

The registry reports geometric means and geometric coefficients of variation for the treatment conditions. It also reports geometric least-squares-mean ratios with 90% confidence intervals for the three comparisons. The analysis population was described as a pharmacokinetic analysis set, with eligibility criteria involving protocol deviations, medication compliance, and valid primary endpoints. The full population description is not reported in the registry record.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

What does a crossover comparison estimate?

In general, a crossover study compares treatment conditions within participants, with treatment order varied across participants. Each participant can act as a reference for their own response, which can reduce the influence of stable differences between people. The analysis must account appropriately for the paired structure and the treatment sequence. The registry identifies this study as a crossover, but the statistical model and its handling of period or sequence effects are not reported in the registry record.

The Part A comparison concerns TF3 versus TF2 under fasting conditions. Parts B and C instead compare fed with fasted administration within TF2 and TF3, respectively. Keeping these questions separate matters: a food-effect estimate for one formulation is not itself an estimate of the difference between formulations.

How should geometric means and ratios be read?

In general, pharmacokinetic measurements such as AUC are often analyzed on a logarithmic scale because their distributions can be right-skewed and multiplicative differences are often more informative than additive differences. A geometric mean summarizes values on that scale and expresses them back on the original scale. A ratio of geometric means expresses one condition relative to its comparator. A value reported as a percentage of a ratio therefore uses 100% as the point at which the two estimated geometric means are equal.

The registry reports geometric least-squares-mean ratios. Least-squares means are model-based estimates, rather than necessarily being simple arithmetic summaries of the raw observations. The precise model used to obtain these estimates is not reported in the registry record, so the model’s adjustment terms cannot be described from the record.

The geometric coefficient of variation is a measure of variability on a multiplicative scale. In general, greater dispersion can reduce the precision of an estimated comparison, all else being equal. It is distinct from the confidence interval around a ratio: the coefficient of variation describes variability in the observations, whereas the interval describes uncertainty in the estimated comparison.

What information does a confidence interval add?

In general, a confidence interval represents uncertainty around an estimate under the assumptions of the statistical procedure. Its endpoints are not a guarantee that the true value lies within that particular interval, and the interval does not establish practical equivalence on its own. Interpretation depends on the prespecified question and, for a bioequivalence claim, the acceptance limits and analysis rules. Those limits and rules are not reported in the registry record.

The registry reports 90% confidence intervals for all three ratios. It does not report p-values for these comparisons. A confidence interval can still be informative without a p-value: readers can see both the estimated ratio and the range of values compatible with the reported analysis. However, the registry record does not specify the method used to calculate the intervals.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. When a model understates variability, standard errors can be too small and confidence intervals too narrow. A suitable model or robust variance method can address this concern, but the appropriate choice depends on the data and design. The registry record does not report whether over-dispersion was assessed or how variability was handled beyond reporting geometric coefficients of variation.

What can sample-size planning illustrations tell readers?

In general, sample-size planning uses assumptions about the target effect, variability, significance level, allocation, and statistical method to estimate how much information a future study might need. A planning illustration based on an observed effect is not an estimate of the trial’s observed power, and it does not establish what assumptions were used in the original protocol. The registry record does not report the trial’s sample-size justification. The planning assumptions described for the illustrations specify a two-sided significance level of 0.05, equal allocation, and a normal approximation; they are not evidence that these were the design assumptions for the trial.

Because this study has multiple parts and comparisons, a single planning figure would not answer every design question. The pharmacokinetic outcomes, crossover structure, and comparisons differ across parts. The registry does not report the trial’s original power target, variance assumptions, or how its overall enrollment was chosen.

10. Analyses Reported by the Sponsor

The registry reports the sponsor’s comparison estimates as geometric least-squares-mean ratios with 90% confidence intervals. For Part A, the reported TF3-to-TF2 ratio is 115.35%, with an interval from 108.55% to 122.58%. For Part B, the fed-to-fasted TF2 ratio is 186.37%, with an interval from 163.61% to 212.28%. For Part C, the fed-to-fasted TF3 ratio is 163.15%, with an interval from 146.17% to 182.10%.

No separate recalculated estimate is reported for these comparisons, and no discrepancy between a recalculation and the registry’s analysis is identified. The sponsor’s reported analyses are therefore the available inferential results to interpret. The analysis method is not reported in the registry record, and the confidence intervals should not be reverse-engineered into a different analysis.

The registry does not report p-values or the acceptance limits used to judge bioequivalence. Consequently, the posted ratio and interval describe the estimated relative exposure and its precision, but they do not independently establish that a formal bioequivalence criterion was met. The original statistical analysis plan and its detailed procedures are not reported in the registry record.

11. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary AUC 0-t endpoint across Parts A, B, and C, as well as secondary pharmacokinetic and safety outcomes. It reports 11 outcome measures and 9 analyses, and lists 8 secondary outcomes. The record does not explain how the analyses were grouped into those counts or how the three primary comparisons were treated for inferential purposes.

When multiple outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase if each is tested separately without adjustment. In general, multiplicity procedures can control this issue, or a study can define a hierarchy of primary questions in advance. Whether either approach was used, and whether any adjustment was made, is not reported in the registry record. No p-values are provided for the three reported AUC comparisons, so the record does not show a multiple-testing procedure for them.

The registry describes a pharmacokinetic analysis set and gives some eligibility criteria, including absence of relevant protocol deviations, adequate trial medication compliance, and valid primary endpoints for both treatments in Part A. The full analysis-population description is incomplete in the registry record. The number of participants excluded from each analysis, the handling of incomplete crossover data, and the rules for missing or below-quantification measurements are not reported in the registry record.

In general, missing observations can affect a crossover comparison if missingness is related to treatment, period, participant characteristics, or the measured response. The consequences depend on the extent and pattern of missingness and on the analysis method. The registry record does not report the amount or pattern of missing endpoint data, any imputation procedure, or sensitivity analyses for missing data.

The method used to derive the reported ratios and confidence intervals is also not reported in the registry record. Without the analysis plan, it is not possible to determine whether sequence, period, or other design factors were included, or how protocol deviations were handled beyond the broad analysis-set description.

12. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

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: femoral neck fracture (7.1%).

The registry reports serious adverse events by treatment condition. It lists no serious events for the Part A TF2 fasted condition (0 of 38), Part A TF3 fasted condition (0 of 40), Part B TF2 fasted condition (0 of 12), Part C TF3 fasted condition (0 of 12), or Part C TF3 fed condition (0 of 12). For Part B TF2 fed, it reports 1 serious adverse event among 14 participants at risk. No deaths are listed for any condition.

The registry also identifies “Femoral neck fracture” as a top serious-event term and associates it with 7.1%. The context and denominator for that percentage are not reported in the registry record, so it should not be treated as a rate for a particular treatment condition without further information.

These are descriptive counts, not estimates of comparative risk. The crossover design means participants may contribute to more than one condition, so condition-level counts do not necessarily represent independent groups. The registry’s counts alone do not establish whether an event was caused by treatment. It also reports non-serious treatment-emergent adverse events, but those counts and serious-event counts should be interpreted separately from the pharmacokinetic results.

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

The results describe tepotinib exposure under three study questions: TF3 compared with TF2 under fasting conditions, and fed compared with fasted conditions for each formulation. The reported ratios and confidence intervals quantify the estimated relative AUC 0-t exposure and its uncertainty in the analyzed participants. The condition-level geometric means and coefficients of variation add descriptive information about exposure and variability.

These findings do not by themselves establish whether TF3 and TF2 satisfy a formal bioequivalence standard. That conclusion requires the applicable acceptance limits and prespecified decision rules, which are not reported in the registry record. The findings also do not provide a direct comparison of clinical outcomes, because the primary endpoint is pharmacokinetic exposure and the participants were healthy subjects.

The food-effect estimates indicate the reported relative exposure for fed versus fasted administration within each formulation. They should not be read as a comparison of TF2 against TF3, nor should they be interpreted as a direct measure of how food changes a clinical outcome. The confidence intervals describe statistical uncertainty, not the range of responses for every individual participant.

The safety counts are limited descriptive observations from the recorded study conditions. They do not support broad conclusions about uncommon harms or comparative safety, particularly because the study was a Phase 1 pharmacokinetic investigation and the condition counts can include participants who experienced more than one condition. No deaths were listed, but this is not evidence that an event could not occur outside the observed study.

More broadly, the registry record does not report the full statistical analysis plan, the sample-size justification, or the detailed handling of missing data. Those omissions limit independent assessment of how the reported estimates were produced and how the study’s decision criteria were applied.

14. Why This Trial Matters Statistically

This study is statistically useful because it separates two related but distinct pharmacokinetic questions. Part A addresses relative exposure between two tablet formulations under fasting conditions. Parts B and C address the effect of food within each formulation. Distinguishing these comparisons helps prevent a food-effect result from being misread as evidence about formulation equivalence.

The crossover design also makes the comparison structure important. In general, within-participant comparisons can account for some stable differences between participants, but interpretation depends on the treatment sequence and period structure as well as appropriate analysis. The registry identifies the crossover design and varied treatment orders, while the detailed model is not reported in the registry record.

Reporting both ratios and confidence intervals gives readers more information than a point estimate alone. The point estimate describes the estimated relative exposure; the interval shows the uncertainty around it. The posted intervals are central to judging precision, but they cannot be evaluated against bioequivalence criteria without the criteria themselves.

The registry also illustrates why analysis-population definitions and missing-data rules matter in pharmacokinetic studies. Different numbers of participants are reported across conditions, and the record gives only a partial description of the analysis set. Clearer reporting of participant flow and analysis methods would help readers understand how the crossover observations contributed to each estimate.

Finally, the safety results should remain in context. The registry reports adverse-event counts, but they do not replace the primary pharmacokinetic comparison, and they should not be used to infer treatment causation or generalize beyond the study population.

15. 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 leaves important interpretive details unspecified. It does not report the bioequivalence acceptance limits, the full statistical analysis plan, or the statistical method used to estimate the geometric least-squares-mean ratios and confidence intervals. It also does not report p-values for the AUC comparisons or explain how multiplicity across the study parts was handled.

The analysis population description is incomplete. The record gives some eligibility requirements for the pharmacokinetic set, but not a complete account of the population used for every comparison. It does not report participant flow by part, the number of missing or invalid endpoint measurements, or how incomplete crossover observations were handled. Condition-specific sample sizes therefore need to be read as analysis counts, not as a full account of enrollment and completion.

The registry reports the study as open-label, and the full procedures for allocation, period effects, and sequence effects are not reported in the registry record. The detailed washout information is also incomplete in the arm descriptions. These details matter when assessing a crossover analysis, even though the design and treatment-order variation are described.

The population is described as healthy subjects, limiting how directly these pharmacokinetic findings can be generalized to other populations. The study’s primary outcome is a plasma exposure measure rather than a clinical outcome. In addition, the safety results are descriptive, and the record does not provide enough context for interpreting the listed serious-event term and its associated percentage by treatment condition.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Bioequivalence of TF3 and TF2 and Effect of Food on the PK of Tepotinib — NCT03629223.
• Registry record last updated 2023-10-10; status last verified 2023-10.
• Results first posted 2023-10-10.
• 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.

19. Record Summary

NCT03629223 is a completed Phase 1 randomized, open-label crossover study of tepotinib tablet formulations TF2 and TF3 and the effect of food on tepotinib pharmacokinetics in healthy subjects. It enrolled 66 participants and had a primary completion date of 2019-01-25.

The primary endpoint was AUC 0-t. The registry reports geometric-mean ratios and 90% confidence intervals for TF3 versus TF2 under fasting conditions and for fed versus fasted administration within each formulation. It also reports condition-level geometric means, variability, and adverse-event counts.

The ratios describe relative pharmacokinetic exposure, but the registry does not report the bioequivalence acceptance limits, the full analysis method, or a complete account of missing data and analysis populations. The reported estimates should therefore be interpreted with those limitations in mind.