23.The sample size of replicate cross-over designs where Cmax acceptance range is widened based on intra-subject coefficient of variation (CV) of the comparator product but AUC acceptance range is the classical 80-125%, should be calculated for Cmax with widening and AUC without widening. Sometimes AUC without widening requires a larger sample size than Cmax with widening.
24. The sample size calculation for a replicate design with widening of the acceptance range should be calculated as described by Tothfalusi and Endrenyi in "Sample Sizes for Designing Bioequivalence Studies for Highly Variable Drugs". J Pharm Pharmaceut Sci 15(1) 73-84, 2012. The conventional methods for replicate designs do not take into account the impact of acceptance range widening on the sample size calculation.
25. The sample size calculation for 2x2 cross-over designs or parallel designs are often not justified adequately or presented with sufficient detail. For more information on sample size calculation see Julious S.A. "Sample sizes for clinical trials with Normal data." Statistics in Medicines 2004; 23: 1921-1986. The sample size should be based on the desired power (e.g., 80 or 90%), consumer risk (5%), pre-defined equivalence margins (usually 80 – 125%), expected difference between formulations (e.g., 5%), and the expected inter-subject variability for parallel designs or intra-subject variability for the cross-over designs.
对于2x2交叉设计或并行设计的样本量计算通常没有充分的理由或没有提供足够的细节。有关样本量计算的更多信息，参见Julious S.A.“具有正常数据的临床试验样本量” Statistics in Medicines 2004; 23: 1921-1986。样本量应基于所需功效（例如，80％或90％）、消费者风险（5％）、预先定义的等效界值（通常为80％至125％）、配方之间的预期差异（例如，5％）以及平行设计的预期受试者间变异性或交叉设计的预期受试者内变异性。
26. The number of subjects that are added to the sample size calculation to compensate for potential dropouts or withdrawals should be realistic and consistent with the study design (e.g., more dropouts expected in longer studies) and tolerability profile of the drug.
27. The sample size calculation is sometimes based on assumptions that are not consistent with differences observed in previous pilot studies and the expected variability based on previous pilot studies or the variability described in the literature.
28. Sample size is sometimes calculated to detect a difference between treatments instead of being based on a calculation aimed to show equivalence.
有时计算样本量是为了检测治疗之间的差异，而不是基于旨在显示等效性的计算。
29. In case of a parallel design, it is extremely important to obtain balanced groups in all demographic characteristics that might impact the pharmacokinetics of the drugs. The methods employed to ensure balanced groups are generally not described in the protocols.
32. The calculation of the 90% confidence interval (CI) of the mean test/comparator ratio for the primary PK parameters should not be confused with the two one-sided t-tests employed to reject the null hypothesis of non-equivalence. The end result is the same, but these are not the same calculations.
33. In cases of two-stage designs, the consumer risk should be adjusted to preserve the type I error at or below 5%. It is not acceptable to use 90% confidence interval in both the interim and the final analyses. Due to the statistical complexity of the alpha level expenditure in two-stage bioequivalence cross-over trials, two stage designs are not encouraged and, if used, the design should be as simple as possible e.g., with equal sizes in both stages. The Applicant should demonstrate that the consumer risk is not inflated above 5% with the proposed design and alpha expenditure rule, taking into account that simulations are not considered sufficiently robust and analytical solutions are preferred.
34. While in cases of 2x2 cross-over or parallel trials only the data of subjects who complete the study can be considered for the pharmacokinetic and statistical comparison, in cases of replicate designs, data from subjects who did not complete all periods of treatment may still be considered. All subjects with two observations of the comparator product should be considered for the calculation of the intra-subject CV of the comparator. Those subjects with at least one observation for the test and one observation for the comparator should be considered for the average bioequivalence assessment.
35. The statistical procedure should be conducted without imputing values to the missing observations.
执行统计程序时，不应将数值推算到缺失的观察值上。
36. In those cases where the subjects are recruited and treated in groups, it is appropriate to investigate the statistical significance of the group-by-formulation interaction e.g., with the following ANOVA model: Group, Sequence, Formulation, Period (nested within Group), Group-by-Sequence interaction, Subject (nested within Group*Sequence) and Group-by-Formulation interaction. If this interaction is significant, the study results are not interpretable. However, it is not considered to be correct to report the results of the 90% confidence interval of the ratio test/comparator based on the standard error derived from this ANOVA. If the group-by-formulation interaction is not significant, the 90% confidence interval should be calculated based on the ANOVA model defined in the protocol. This model may or may not include the group effect as pre-defined in the protocol. This depends on whether the group effect is believed to explain the variability observed in the data.
37. The a posteriori power of the study does not need to be calculated. The power of interest is that calculated before the study is conducted to ensure that the adequate sample size has been selected. Furthermore, the calculated power is often the power to detect differences, which is not relevant. The relevant power is the power to show equivalence within the pre-defined acceptance range.
38. In case of multiple comparisons, the consumer risk should be adjusted. Another option is a hierarchical approach, where it is required first to show BE in the easiest or most desired comparison (e.g., when a dispersible tablet is administered with a glass of water) and if bioequivalence is shown, then the second comparison is performed (e.g., when the dispersible tablet is administered dispersed in the glass of water). However, if the first comparison is not able to show equivalence, the second is not conducted.
39. In case of dose-normalization when the same dose is not administered in both treatments, it is not necessary to normalise all PK values individually. It is possible to dose-normalise only the point estimate of the ratio T/R used for the calculation of the 90% CI. Dose-normalisation of the point estimate of the test/comparator ratio in log scale is done by adding the ln(dose of comparator/dose of test).
40. It is not necessary to calculate the non-parametric 90% CI of Tmax. A numerical comparison of the median values and its range is considered sufficient.
不必计算Tmax的非参数90％CI。中值及其范围的数值比较被认为是足够的。
EXCLUSION OF DATA 数据排除
41. In order to exclude the pharmacokinetic results of those subjects who vomit during the study, the protocol should define in hours the value of two times median Tmax (as documented in the literature) since the decision to exclude or include the subject should be made before analysing the study samples and as soon as possible, when emesis occurs. This time may differ for different drugs of a fixed dose combination.
42. Statistical tests to identify "outlier observations" are not acceptable in case of parallel or 2x2 cross-over designs. Therefore, these tests should not be conducted. In case of replicate cross-over designs where the acceptance range is widened based on the intra-subject CV of the comparator product, outliers may inflate the estimation of intra-subject variability of the comparator and outliers should be investigated. The outliers of interest in case of a replicate design are not those subjects that are discordant with the rest of subjects, because if the subject behaves in a similarly discordant way in both periods, the behaviour is confirmed. The outliers of interest in a replicate design are those that behave differently in the periods where the comparator product is replicated and, consequently, inflate the intra-subject variability of the comparator product. Then, the application of a conventional statistical test is not sufficient to detect the outliers and the type of outlier should be discussed. In any case, a sensitivity analysis with and without the detected outliers is considered essential to assess the impact of the outliers.
43. Re-dosing in case of suspected outliers is not considered acceptable as a method to confirm the outlier behaviour of the subject.
如果怀疑存在离群值，则重新给药不被认为是确认受试者离群值表现的方法。
44. The clinical and analytical investigations conducted for suspected outliers are usually conducted only in the subjects that are considered as outliers or at least with more emphasis on those subjects, and this is not considered correct because all subjects should be treated equally. The findings that may justify an outlier behaviour might be found also in subjects that do not behave as outliers if these subjects are investigated in a similar fashion.
45. The exclusion from statistical analysis due to very low concentrations observed following administration of the comparator product requires the pre-definition of what is considered to be 'very low' in the protocol (e.g., in accordance with EMA guideline, <5% of the geometric mean of the other subjects).
46. A single missed blood sample should not be considered as a reason for the exclusion of a subject by the principal investigator. If such a decision is to be made, it must be made prior to the initiation of the bioanalytical portion of the study.
47. Subjects with Cmax in the first sampling point should not necessarily be excluded. The study should be designed so Cmax does not occur at the first sampling time, but if that happens only in a small number of profiles the data can still be considered.
48. The samples of subjects that do not finish the study because of an adverse event should be measured for safety reasons in order to investigate whether the withdrawal was related to unexpectedly high drug concentrations causing the adverse events.
49. Subjects should not be excluded simply because three consecutive sampling points are missing.
不应仅仅因为缺少三个连续的采样点而排除受试者。
BIOANALYTICAL METHOD 生物分析方法
50. The list of parameters for the validation of the bioanalytical method that are included in the clinical protocol is often not complete.
临床方案中包含的用于验证生物分析方法的参数列表通常不完整。
51. Incurred sample reanalysis (ISR) does not need to be conducted in 7% of the study samples exceeding 1,000 samples, 5% of these samples is sufficient.
无需对超过1,000个样本的7％研究样本进行样本再分析（ISR），分析5％的样本就足够了。
52. ISR samples should not be selected based on concentrations above the low QC.
不应根据高于低QC浓度而选择ISR样品。
53. Manual integration should be performed only when the instrument is not able to correctly integrate the peak with the default settings and it cannot be solved by refining the settings such as the expected retention time.
54. Plasma samples from subjects that dropout or are withdrawn due to an adverse event should be analysed for a complete safety analysis of the data, in order to assess if the dropout or withdrawal is due to an adverse event that might be related to high concentrations. These data should not be considered for efficacy or bioequivalence analysis but, they are supportive for the safety analysis.
55. The protocol should include the centres where the study is going to be conducted.
方案应包括将要进行研究的中心。
56. All studies should be monitored. It is not acceptable to state that the study may be monitored at the discretion of the sponsor by any of its representatives.
所有研究应受到监测。声称由申办人的任何代表酌情对研究进行监测是不可接受的。
57. Monitoring and auditing activities should not be confused because they are different activities. Monitoring is conducted by the sponsor or a CRO contracted by the sponsor and the audits are performed by the centre where the study is conducted.
