The main considerations in the review of statistical analysis 
methods include the following:

1. Primary statistical hypothesis: The statistical hypothesis should be developed based on the purpose of the study. Usually the primary hypothesis is developed specifically for the primary efficacy endpoint.
2. The overall Type I error rate should be controlled at 0.025 for a one-sided test and 0.05 for a two-sided test. When multiplicity is present, appropriate statistical adjustments should be implemented to prevent Type I error inflation. Multiplicity may arise, for example, from multiple primary endpoints, multiple comparisons of treatments, repeated evaluation over time and/or interim analyses, etc. 
3. Adjustment for baseline covariates in clinical trials.If the random allocation process has been performed correctly, the known and unknown baseline prognostic variables will be balanced between treatment groups. Specifically, the evaluation of efficacy is to assess the improvement from baseline for each subject, unless stated otherwise, the baseline information should be incorporated in the analysis, and the baseline-by-treatment interaction should be explored when necessary. In addition, factors that may confound the efficacy, e.g., the randomization stratification factor(s) should normally be included as covariates in the primary analysis. For both unadjusted and adjusted results, the analysis that will represent the primary analysis and the covariates to be included in the primary analysis must be pre-specified in the protocol.
4. The methods to analyze the primary efficacy endpoint should be adequate to prevent bias.For example, if a paired sample was analyzed using independent tests, the results of the analysis may be incorrect or misleading. Another example would be that in survival analysis, if censoring and time are ignored and only the binary outcome of whether the event occurred or not is considered, the true efficacy results will not be adequately presented. 
5. Point estimates and confidence intervals.The primary efficacy analysis should provide not only the hypothesis test results, but also the point estimates and the corresponding 95% confidence intervals of the primary efficacy endpoint. This is particularly crucial in clinical effectiveness assessments of new drugs.

The statistical methods for dealing with missing data for the primary efficacy endpoint, as well as the questionnaire endpoints, should be clearly defined in the protocol. The review considerations will focus on whether the proposed missing data handling method is appropriately chosen for the study design and the primary efficacy endpoint, and whether the proposed method is considered to be a conservative approach. For example, if the primary efficacy endpoint is the change from baseline in HbA1c, and the primary efficacy analysis population is intent-to-treat (ITT).

If missing data is not entered, then subjects with missing data will not be included in the primary efficacy analysis. Ignoring these subjects in the analysis will violate the ITT principle and is not considered acceptable in general. Another example is a hepatitis B clinical trial. The primary efficacy endpoint is the proportion of subjects with HBV DNA < 29 IU/mL at Week 48 and subjects with missing data at Week 48 will be treated as failures, regardless of the presence or absence of hepatitis B e-antigen status at baseline.

For this case, if the dropout rates differ between the two groups, the proposed method may not be a conservative approach under certain circumstances. Thus, in addition to the primary method of handling missing data, appropriate sensitivity analyses should be carried out to investigate the robustness of the study conclusions. If inconsistency of the results between the primary and sensitivity analyses is observed, the effects on the conclusions of the trial must be discussed.

1. Definition of analysis populations: The set of subjects whose data are to be included in the analyses should be clearly defined in the protocol, e.g. the intent-to-treat (ITT) and the per-protocol (PP) population.
2. The primary population for efficacy analysis: In Phase III confirmatory trials, the primary population for efficacy analysis should be clearly specified in the protocol. In general, the more conservative analysis population should be used for primary efficacy analysis. In superiority trials, the ITT analysis should be considered primary and the PP supportive. However, use of the ITT population is generally not conservative in a non-inferiority/equivalence trial. The CPMP guideline suggests that in a non-inferiority/equivalence trial, both the ITT and PP populations have equal importance and their use should lead to similar conclusions for a robust interpretation. Thus, it is recommended to perform sensitivity analyses using different analysis populations. If significant different findings are noted, further explanation and discussion will be required. 

Long-term clinical trials aimed at life-threatening indications often adopt the group sequential design in performing interim analysis. Interim analysis may be conducted for efficacy or for safety. Generally speaking, if it is only for safety monitoring, the results will not lead to early stopping of a trial and therefore it is not necessary to specify trial stopping rules in the trial protocol. If interim analysis can lead to early stopping of a trial, stopping rules set for efficacy usually are more stringent than for safety. Statistical review considerations for interim analysis include the following:

1. Procedure and method of interim analysis: The method used for early stopping of a trial, for example, Pocock (1977) or O’Brian-Fleming (1979) procedures, the timing and frequency of interim analysis, and the stopping boundary derived accordingly for each interim analysis should be clearly stated in the trial protocol. However, pre-specification of the timing and frequency of interim analysis can be exempted if the Lan-DeMets (1994) α spending function procedure is adopted for trial early stopping.
2. Independent Data Monitoring Committee (IDMC): In principle, the IDMC is composed of external clinical and statistical experts who are not affiliated with the sponsor and trial investigators. In addition to monitoring trial safety, the Committee is also in charge of interim analyses. For each interim analysis, the Committee will propose to sponsor a decision to continue or stop the trial early based on the interim statistical analysis results and considerations of all aspects.
3. Overall Type I error (α) control: If early stopping of a trial for strong efficacy is allowed for interim analysis, the chance of a Type I error increases as the frequency of the interim analysis increases. The nominal Type I error rate for each interim analysis should be adjusted so that the overall Type I error rate is controlled below 0.05 (two-sided). However, if the trial is designed to allow early stopping for poor efficacy (futility), the setting of the futility boundary is generally not included in the consideration of the Type I error adjustment.
4. Adaptive design based on interim analysis: If based on interim analysis results, the parameters and assumptions for sample size calculations may need to be updated, or sample size re-estimation may be performed; or the study design may even be changed from superiority to non-inferiority, this should be pre-specified in trial protocol principally the plan of the adaptive design.

Sample size determination depends on the objective of clinical trials. In general, Phase I clinical trials are not required to estimate the sample size, but the trial protocol should indicate the maximum number of participants be enrolled and it must comply with the regulatory requirements of Taiwan. If a Phase II early exploratory clinical trial is designed, unless it is indicated for the treatment of life-threatening disease (e.g. cancer), sample size estimation is usually not required.

The sample size should be considered and estimated in a Phase III efficacy confirmatory trial. The considerations for regulatory statistical review include: the sample size is estimated based on the primary endpoint parameters, the parameters are supported by references, the statistical hypothesis for sample size estimation is developed based on trial objective and clinical assumptions, the effect size is achievable and clinically meaningful, the statistical method used for sample size estimation is appropriate, and there is sufficient power to detect the claimed efficacy.

A non-inferiority/equivalence design is often adopted in a concurrent active-controlled clinical trial, if the control drug is considered as a standard therapy. The margin of this type of design must be pre-defined in the trial protocol. The pre-determined threshold should retain 50% or more of the efficacy of the control drug and the efficacy superior to placebo remains confirmed. In addition, the retained efficacy should also exhibit clinical meaningfulness.

1. Adequacy of randomization method: A clinical trial with a control group should adopt a proper randomization procedure to assign subjects to different treatment groups. The timing of randomization is a critical issue in a trial with different time periods (e.g., screening period, run-in period, and treatment period). In small trials with important prognostic factors, the use of stratification can be especially essential for the review. The randomization procedures should be organized centrally in multicenter trials.
2. Use of a blinding procedure: A double-blind trial provides the most rigorous scientific evidence. If a double-blind trial is not feasible, then the single-blind option should be considered. In some cases only an open-label trial is practically or ethically possible, for example, trials involving the comparison of different routes of administration (oral vs. intravenous) or those necessitating surgery. Single-blind and open-label trials provide additional flexibility, but how to minimize the potential biases in the conduct and interpretation of a clinical trial is always a concern. For these trials, primary endpoints should be as objective as possible and centralized randomization method should be applied. If the endpoint is subjective, use of evaluator-blinding should be considered.
3. Choice of a control group: Scientifically, concurrent placebo-controlled trials provide the most convincing evidence of efficacy. In cases where an available treatment is known to prevent serious harm, such as death or irreversible morbidity in the study population, it is more appropriate to use an active concurrent control. Considerations should be paid to the selection of the dose and regimen of the active comparator. The use of historical controls is inappropriate for most circumstances. In limited cases, historical controls would be acceptable. For example, there is no standard treatment, very low response rates in the standard treatment, or if the study population is very limited. In cases where a historical control is used, it is encouraged to consult with the Center for Drug Evaluation, Taiwan.
4. Adequacy of using a crossover design: Most clinical trials involve parallel treatment designs where a subject is randomly assigned to receive only one of the treatments. In certain cases, a crossover design may be useful if a drug effect develops rapidly and subjects return to baseline conditions quickly after cessation of therapy. In the crossover design, each subject is randomized to receive a sequence of two or more treatments. The subject serves as his or her own control and the variability of the response to the treatment is correspondingly reduced, allowing detection of effect size with reduced sample size. When a crossover design is used, the review considerations include whether the indication claimed by the study drug is a chronic stable and reversible disease; whether the efficacy of the study drug can be presented within a single time period, and whether the washout period is long enough to avoid carryover effects.

1. The primary endpoint should be established based on the primary objective of the trial. The primary endpoint should be well-defined in the study protocol, along with the rationale, method of assessment and timing of assessment. For example, if the primary endpoint is defined as the changes in the sitting diastolic blood pressure, whether the definition refers to the percentage of change in blood pressure, or the absolute value of the blood pressure change should be clearly specified. 
2. The method for measurement of the primary endpoint should be appropriate and should not introduce bias. For example, if the primary endpoint is seizure frequency, it is highly likely to be affected by the length of time during which the subject is being observed. Thus the period over which seizure frequency is measured should be pre-specified and the outcome of seizure might be standardized (e.g., standardized seizure frequency per 28 days over the 12-week maintenance period).
3. When direct assessment of clinical benefit is not feasible or practical, indirect measurement of effect (surrogate endpoints) may be considered as the primary endpoint in clinical trials. A surrogate endpoint is used as a primary endpoint when the surrogate endpoint is well-validated and is well known to predict clinical outcome. For example, in a confirmatory oncology study a proper justification for the use of progression free survival as a surrogate for overall survival should be provided. 
4. If multiple primary endpoints are planned, the effect on the Type I error should be explained because of the potential multiplicity problems; the method of controlling Type I error should be specified in the protocol.

The main considerations for the statistical review of IND applications are as follows:

1. Choice of primary endpoint
2. Choice of study design 
3. Sample size estimation
4. Choice of non-inferiority or equivalence margin 
5. Interim analysis and early stopping 
6. Analysis sets for efficacy and safety
7. Method of handling missing values
8. Method of statistical analysis and adjustment of significance