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BIOSTATISTICAL METHODOLOGY IN CLINICALTRIALS

Guideline Title Biostatistical Methodology in Clinical TrialsLegislative basis Directive 75/318/EEC as amendedDate of first adoption May 1993Date of entry intoforce

October 1993

Status Last revised May 1993Previous titles/otherreferences

Biostatistical methodology in clinical trials in applicationsfor Marketing Authorisations for Medicinal Products/III/3630/92,

Additional Notes This note for guidance concerns the application of Part 4,sections C and F of the Annex to Directive 75/318/EEC asamended with a view to the granting of a marketingauthorisation for a medicinal product. It is intended togive support to applicants when designing, conducting,documenting, evaluating and reporting clinical trials ofnew medicinal products in the context of their overallclinical development. It is written primarily toharmonise the biostatistical methodology applied toclinical trials within member states, during both clinicaldevelopment and subsequent review.

CONTENTS

1. INTRODUCTION

2. OVERALL DEVELOPMENT CONSIDERATIONS

3. CLINICAL TRIAL DESIGNS

4. OTHER DESIGN ISSUES

5. THE SAMPLE SIZE

6. THE POPULATION

7. DESIGN TECHNIQUES TO AVOID BIAS

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8. PRIMARY AND SECONDARY VARIABLES

9. THE CASE REPORT FORM

10. PRE SPECIFIED DATA ANALYSIS

11. THE CONDUCT AND MONITORING PHASE

12. INTEGRITY OF DATA AND COMPUTER SOFTWARE

13. EVALUATION AND REPORTING

14. OUTLINE OF SAFETY ISSUES

15. SUMMARISING THE CLINICAL DATABASE

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BIOSTATISTICAL METHODOLOGY IN CLINICALTRIALS

1. INTRODUCTIONThis note for guidance should be read in the light of Directive 75/318/EEC as amended whichsets up the relevant regulatory framework. It should also be read in conjunction with note forguidance on Good Clinical Practice (GCP) and which emphasises the importance of statisticalprinciples and expertise in the design, conduct and analysis of clinical trials.

This Note is intended to give support to applicants when designing, conducting,documenting, evaluating and reporting clinical trials of new medicinal products in thecontext of their overall clinical development. It will also assist scientific experts chargedwith preparing Expert Reports or assessing evidence of efficacy and safety, principally fromPhase III clinical trials. It is written primarily to harmonise the biostatistical methodologyapplied to clinical trials within member states, during both clinical development andsubsequent review. It is largely concerned with planning and methodology, and does notattempt to cover systematically the structure and content of clinical reports which is coveredin the note for guidance on Structure and Content of Clinical Reports.

The efficacy and clinical safety of medicinal products must be demonstrated by clinicaltrials which follow the guidance given in GCP. Within this document biostatistical issuesare clearly identified as an integral part of the design and conduct of clinical trials.Biostatistical principles underlie the multi-disciplinary approach necessary to ensure thatclinical trials provide adequate evidence to support the decisions which rest upon them and,therefore, an appropriately qualified and experienced statistician should be responsible foreach clinical trial at all stages from design through to reporting.

In the early phases of product development many clinical trials are of an exploratory nature.Some of the content of this note is strictly relevant only to confirmatory trials such as thepivotal trials carried out in the later phase of development (late Phase II / Phase III) in orderto give definitive proof of efficacy, and these trials are certainly the main target of thestatistical material covered here. Nevertheless, biostatistical considerations are relevant toall clinical trials; hence the substance of this note should be applied as far as possible to al lphases of product development and to all types of study. In section 14 of this note for guidancea brief outline of some of the statistical issues relevant to safety evaluation is given.However, a separate guideline will be necessary to cover this topic fully.

This note for guidance is intended:

• to outline the relevant principles of design and analysis,

• to describe generally appropriate approaches to these tasks,

• to describe some approaches which should not be adopted,

• to set conventions where choice would otherwise be entirely arbitrary. It is not intendedto give detailed (textbook or “cookbook”) specification of methodology, thus leavingapplicants and other users responsible for making reasoned choices between

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alternative statistical approaches and procedures to solve specific problems. This maysometimes require innovation.

All important details of the design, conduct and proposed analysis of each clinical trialcontributing to a marketing authorisation application should be clearly specified in aprotocol written before the trial begins. Any subsequent changes to the protocol, and thereasons behind them, should be carefully documented. The clinical trial protocol and allsubsequent amendments should be signed and dated by the responsible personnel (includingthe trial statistician). The trial statistician should ensure that the protocol covers all relevantstatistical issues clearly and accurately, using technical terminology as appropriate.

Although this note for guidance is written largely from the classical (frequentist) viewpoint,the use of Bayesian or other well-argued approaches is quite acceptable.

2. OVERALL DEVELOPMENT CONSIDERATIONS

2.1 Clinical development plan

The broad aim of the process of clinical development of a new active substance is to find outwhether there is a dose range and schedule at which the substance can be shown to besimultaneously effective and safe, to the extent that the risk/benefit relationship isacceptable. The particular patients who benefit from the medicinal product, and the specificindications for its use, also need to be defined.

Satisfying these broad aims usually requires an ordered programme of clinical trials, eachwith its own specific objectives. This should be specified in a clinical plan, or a series ofplans, with appropriate decision points and flexibility to allow modification as knowledgeaccumulates. An application for marketing authorisation should clearly describe the maincontent of such plans, and the contribution made by each trial. Interpretation andassessment of the evidence from the total programme of trials involves synthesis of theevidence from the individual trials (see Section 15). This is facilitated by ensuring thatcommon standards are adopted for a number of features of the trials such as dictionaries ofmedical terms, definition and timing of the main measurements, handling of protocoldeviations and so on. A formal statistical overview or meta-analysis may be informativewhen medical questions are addressed in more than one trial. Where possible this should beenvisaged in the plan so that the relevant trials are clearly identified and any requiredcommon features of their designs are specified in advance.

Other major statistical issues (if any) which are expected to affect a number of trials in acommon plan should be addressed in that plan.

2.2 Confirmatory studies

As a rule, confirmatory trials are necessary for the definitive proof of efficacy. In suchtrials the key hypothesis of interest is always pre-defined, and corresponds to the hypothesiswhich is subsequently tested when the trial is complete. However, in a confirmatory trial itis equally important to estimate with due precision the size of the effects attributable to thetreatment of interest and to relate these effects to their clinical significance.

Confirmatory trials are the cornerstones of decision making and hence adherence to theirplanned design and procedures is particularly important; unavoidable changes must beexplained and documented, and their effect examined. A detailed and justified account of

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the design of each such trial, and of all other statistical aspects such as the plannedanalysis, should be set out in the protocol. Each trial should address only a limited numberof questions.

Firm evidence of efficacy requires that the results of the pivotal confirmatory trialsdemonstrate that the medical product under test has unequivocal clinical benefits. Thenumber of pivotal trials should therefore be sufficient to answer each key clinical questionrelevant to the efficacy claim clearly and definitively. In addition it is important that thebasis for generalisation to the intended patient population is understood and explained; thismay also influence the number of pivotal trials required. Replication of important studies i sof great value during the interpretation of results, especially when unforeseen problems havearisen during conduct or analysis or when earlier studies provide an insecure basis for themain hypothesis to be tested.

2.3 Exploratory studies

The rationale and design of confirmatory studies nearly always rests on earlier clinicalwork carried out in a series of exploratory studies. Like all clinical trials, these exploratorystudies should have clear and precise objectives. However, in contrast to confirmatorystudies, their objectives may not always lead to simple tests of pre-defined hypotheses. Inaddition, exploratory studies may sometimes require a more flexible approach to design sothat changes can be made in response to accumulating results. Their analysis may entaildata exploration; tests of hypothesis may be carried out, but the choice of hypothesis may bedata dependent. Such studies cannot be the basis of the formal proof of efficacy, although theymay contribute to the total body of relevant evidence.

Any individual study may have both confirmatory and exploratory aspects. For example, i nmost confirmatory studies the data are also subjected to exploratory analyses which serve asa basis for explaining or supporting their findings and for suggesting further hypotheses forlater research. The protocol should make a clear distinction between the aspects of a studywhich will be used for confirmatory proof and the aspects which will provide data forexploratory analysis.

3. CLINICAL TRIAL DESIGNS

3.1 The parallel group design

The most common design of clinical trial in Phase III is the parallel group design in whichpatients are randomised to one of two or more arms, each arm being allocated a differenttreatment. These treatments will include the new medication under investigation, at one ormore doses, and one or more control treatments, such as placebo and/or an activecomparator. In general terms, the analysis of such trials and the interpretation of theirresults is straight-forward and is described in standard statistical textbooks. However, evenin this relatively simple situation biostatistical advice is still necessary (in accordance withGCP), because there may be additional features of the design which it is important oressential to take into account, but which complicate the analysis and interpretation (e.g.covariates, repeated measurements over time, interactions between design factors).

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3.2 The cross-over design

In the cross-over design of clinical trial, each patient is randomised to a sequence of two ormore treatments, and hence acts as his/her own control for treatment comparisons. Thissimple manoeuvre is attractive primarily because it reduces the number of patients requiredto achieve a specific power, sometimes to a marked extent. In the simplest 2x2 cross-overdesign, each patient receives each of two treatments in randomised order in two successivetreatment periods, often separated by a washout period. The most common extension of thisentails comparing n(>2) treatments in n periods, each patient receiving all n treatments.Numerous variations exist such as designs in which each patient receives a subset of n(>2)treatments, or ones in which treatments are repeated within a patient.

Cross-over designs have a number of problems which can invalidate their results. The chiefdifficulty concerns carryover, that is the residual influence of treatments in subsequenttreatment periods. In an additive model the effect of unequal carryover will be to bias directtreatment comparisons. In the 2x2 design the relevant contrast is totally aliased with theinteraction between treatment and period and, what is more, the test for either of these lackspower because it is a "between patient" contrast. This problem is less acute in higher orderdesigns, but cannot be entirely dismissed.

When the cross-over design is used it is therefore important to avoid carryover. This is bestdone by selective and careful use of the design on the basis of adequate knowledge of both thedisease area and the new medication. The disease under study should be chronic and stable.The relevant effects of the medication should develop rapidly and be completely reversible.The washout periods should be sufficiently long for residual effects to have disappeared. Thefact that these conditions are likely to be met should be established in advance of the trial bymeans of prior information and data.

A common, and generally satisfactory, use of the 2x2 cross-over design is to demonstrate thebioequivalence of two formulations of the same medication in healthy volunteers. Here, theCPMP note for guidance on Investigation of Bioavailability and Bioequivalence gives detailedadvice on how to plan, conduct and evaluate such trials. In this particular application i nhealthy volunteers, carryover effects are rather unlikely to occur if the wash-out timebetween the two periods is sufficiently long. However it is still important to check thisassumption during analysis on the basis of the data obtained, for example by demonstratingthat no substance is detectable at the start of each period.

There are additional problems which need careful attention in cross-over trials. The mostnotable of these are the complications of analysis and interpretation arising from the loss ofpatients, and the difficulties of assigning those adverse events which occur in latertreatment periods to the appropriate treatment. These, and other issues, are described in theguidelines on Dose Response Information to Support Product Authorisation prepared withinthe International Conference on Harmonisation process. The cross-over design shouldgenerally be restricted to situations where losses of patients from the trial are expected to besmall.

3.3 Factorial designs

In a factorial design two or more treatments are evaluated simultaneously in the samepatient population through the use of varying combinations of the treatments. The simplestexample is the 2x2 factorial design in which patients are randomly allocated to one of thefour possible combinations of two treatments, A and B say. These are: A alone; B alone; both

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A and B; neither A nor B. The usual intention of using this 2x2 design is to make efficientuse of clinical trial patients by evaluating the efficacy of the two treatments with the samenumber of patients as would be required to evaluate the efficacy of either one alone. Thesuccess of this approach depends upon the absence of any relevant interaction betweentreatments A and B so that the effects of A and B on the primary efficacy variables follow anadditive model, and hence the effect of A is virtually identical whether or not it is additionalto the effect of B. As for the cross-over trial, evidence that this condition is likely to be metshould be established in advance of the trial by means of prior information and data. Inprinciple this design may also be used for the specific purpose of examining the interactionof A and B to look for non-additivity, but then the advantages of efficiency no longer applybecause much larger trials are necessary to detect clinically relevant interaction. The 2x2design has proved to be particularly valuable for very large mortality studies.

Another important use of the factorial design is to establish the dose response characteristicsof a combination product e.g. one combining treatments C and D. A number, m, of doses of Cis selected, usually including a zero dose (placebo), and a similar number, n, of doses of D.The full design then consists of mn treatment groups, each receiving a differentcombination of doses of C and D. The resulting estimate of the response surface may then beused to help to identify an appropriate combination of doses of C and D for clinical use.

In the clinical development of medicinal products there are a number of other situationswhere these and other factorial designs are occasionally appropriate. The detailed designand analysis of these studies is a matter for professional statistical attention.

4. OTHER DESIGN ISSUES

4.1 Multicentre trials

A multicentre trial is an accepted way of establishing the efficacy of a new medication moreefficiently. Sometimes it provides the only means of accruing sufficient patients within areasonable time-frame. A further advantage commonly claimed for the multicentre trial i sthat it provides a better basis for subsequent generalisation of findings, because the patientsare recruited from a wider population, and the medication is administered in a broaderrange of clinical settings, thus presenting an experimental situation which is more typicalof future use. In addition the involvement of a larger number of investigators gives thepotential for more clinical judgement concerning the value of the medication.

The additional efficiency of the multicentre trial depends upon the assumption that thedifferences between the compared treatments are constant from centre to centre; duringanalysis, the robustness of the conclusions to this assumption generally needs to be explored.It is important to design and conduct the trial with this background in mind. Proceduresshould be standardised as completely as possible: variation of evaluation criteria andschemes can be reduced by investigator meetings, by the training of personnel in advance ofthe study and by careful monitoring during the study. Good design should ensure a balanceddistribution of patients to treatments within each centre and good management shouldensure that centres do not diverge excessively in the number of patients entered. Failure totake these precautions, combined with doubts about the homogeneity of the results, may, i nsevere cases, reduce the value of a multicentre trial to such a degree that it cannot beregarded as giving convincing evidence for the applicant's claims.

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The analysis plan (see Section 10) for a multicentre trial should clearly define the centres(e.g. by investigator, location or region) in the context of the particular trial whenever thereis room for doubt. The plan should also specify prospectively any intention to combine smallcentres in the analysis, and the rules for so doing. The statistical model to be adopted for thecomparison of treatments should be described in the protocol. The model should generallyallow for centre differences – exceptions relate, for example, to large mortality studies withvery few patients per centre – and similarly the possibility of qualitative or quantitativecentre by treatment interaction should generally be explored, as this may affect thegeneralisability of the conclusions.

4.2 Trials to show superiority

Scientifically, efficacy is most convincingly established by demonstrating superiority toplacebo in a placebo-controlled trial. Similarly, efficacy would normally be supported byshowing superiority to an active control treatment. This type of trial is later referred to as a“comparative” trial (see Section 10.1.3).

4.3 Trials to show equivalence

When placebo-controlled trials are considered unethical, however, the demonstration ofcomparable efficacy to that of a standard therapy (rather than superiority) may also beacceptable provided a suitable standard therapy exists. [An example of a suitable standardtherapy would be a widely used therapy whose efficacy in the relevant indication has beenclearly established and quantified in well designed and well documented placebo-controlledtrial(s).] This type of trial is often called an “equivalence” trial. In some indicationsequivalence trials are also undertaken for other regulatory reasons (see, for example, notefor guidance on Clinical Requirements for Locally Applied, Locally Acting Products, containingKnown Constituents). Equivalence trials may also incorporate a placebo thus pursuing twogoals in one trial i.e. establishing superiority to placebo and evaluating the degree ofsimilarity to a reference treatment.

There are well known dangers associated with the use of the active control equivalence trial.These relate to the implicit lack of any yardstick of internal validity (in contrast to placebo-controlled trials), thus making external validation necessary. The equivalence trial is notconservative in nature, so that most flaws in the design or conduct of the trial will tend tobias the results towards a conclusion of equivalence. For these reasons a number of designfeatures need special attention.

First and foremost, it is vital that the protocol of a trial designed to demonstrate equivalencecontains a clear statement that this is its explicit intention. Secondly, the primarymeasurement should be one which has been shown to be valid and reliable, and to reflect themajor aspect of the disease which the new treatment is intended to improve. Thirdly, thedose(s) selected for study, the patient population and other aspects of the design should besuch as to ensure adequate sensitivity of the trial to detect relevant differences if present.Reassurance on this (and other issues) can often be gained by modelling the study on earlierplacebo-controlled studies of the active comparator in which the comparator clearlydemonstrated clinically valuable efficacy. Finally, classical hypothesis testing (with thenull hypothesis that there is no difference between the treatments) is inappropriate, so thatsample size calculations need an alternative basis (see Section 5).

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There are also special issues in analysis. Patients who withdraw or drop out from treatmentcan bias the results towards showing equivalence, and hence the “intention to treat” strategyis insecure (see Section 10.1). Analysis is generally based around the use of confidenceintervals (see Section 10.4) and is directed at establishing the largest possible treatmentdifference which might reasonably be consistent with the observed results.

4.4 Dose Response designs

How response is related to the dose of a new substance is a question to which answers may beobtained in all phases of development, and by a variety of approaches. Dose response studiesmay serve a number of objectives, amongst which the following are of particularimportance: the confirmation of efficacy; the investigation of the shape and location of thedose response curve; the estimation of an appropriate starting dose; the identification ofoptimal strategies for individual dose adjustments; the determination of a maximal dosebeyond which additional benefit would be unlikely to occur. These objectives need to beaddressed using the data collected at a number of doses under investigation, perhapsincluding a placebo (zero dose). For this purpose the application of estimation procedures,including the construction of confidence intervals, and of graphical methods is as importantas the use of statistical tests. The hypothesis tests which are used may need to be tailored tothe special ordering of study arms or to the particular questions of interest in these studies:does response increase monotonically with dose?; does response plateau or decline at higherdoses? The details of the planned statistical procedures should be laid down in the protocol.

4.5 Group sequential designs

The group sequential design is the most commonly applied form of sequential design. Thepurpose of a group sequential design is to allow the trial to be monitored at specific timeintervals so that a treatment arm, or the entire trial, may be stopped early if there is clearevidence of efficacy or of unacceptable adverse effects. Trials may also be stopped earlybecause the chance of ever showing a clinically valuable benefit is assessed as too small.However, the logistics of a group sequential trial are complicated and require carefulplanning: an independent monitoring committee must generally be employed: the statisticalprocedures must be fully specified in advance (see Section 11.4) by the monitoring committeebefore they conduct their first interim look at the data. This design is best reserved for largelong-term trials of mortality or major non-fatal end-points.

5. THE SAMPLE SIZEThe number of patients in a clinical trial should always be large enough to provide areliable answer to the questions addressed, but should also be the minimum necessary toachieve this aim. This number is usually determined by the primary efficacy objective of thetrial. If the sample size is determined on some other basis, then this should be made clearand justified. For example, a trial sized on the basis of safety questions or requirements willusually need larger numbers of patients. (See, for example, note for guidance on The Extentof Population Exposure to assess Clinical Safety for Medicines intended for Long-termTreatment of Non-life-threatening Conditions.)

The usual method for determining the appropriate sample size requires specification of aprimary variable, the test statistic, the null hypothesis, the alternative (‘working’) hypothesis

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(embodying consideration of the treatment difference to be detected or rejected), theprobability of erroneously rejecting the null hypothesis (the type I error), and the probabilityof erroneously accepting the null hypothesis (the type II error), as well as the approach todealing with dropouts and other protocol deviations. The method by which the sample size i scalculated should be given in the protocol, together with the estimates of any quantities usedin the calculations (such as variances, mean values, response rates, difference to bedetected). The basis of these estimates should also be given; in confirmatory studies, theyshould normally be based on published data or on the results of earlier studies. Thetreatment difference to be detected may be based on a judgement concerning the minimaleffect which has clinical relevance in the management of patients, or on a judgementconcerning the anticipated effect of the new treatment, where this is larger. Conventionallythe type I error is set at 5% or less; the precise choice of value is influenced by the priorplausibility of the hypothesis under test and the desired impact of the results. The type IIerror is conventionally set at 20% or less; it is in the investigator's interest to keep thisfigure as low as possible especially in the case of studies which are difficult or impossible torepeat.

When the variance of the primary variable, or the control response rate, is particularlyuncertain, it may be worthwhile to carry out a suitably blinded interim estimation of thequantity in question in order to update the sample size appropriately. Any such plans shouldbe carefully described in the protocol – the steps taken to preserve blindness should beexplained, together with the consequences (if any) for the type I error and the width ofconfidence intervals. (See also Section 11.3).

Sample size calculations should make appropriate allowance for dropouts and any otheranticipated protocol deviations which may affect power. Not only should the sample size beincreased to offset the loss of patients from the study or from their intended treatments, but italso should allow for the fact that the size of effect observed may be reduced by the need toinclude any available data from treatment failures or other early terminators in anintention-to-treat analysis (see Section 10.1.1).

The sample size of an equivalence trial (see Section 4.3) should normally be based on theobjective of obtaining a confidence interval for the treatment difference which is sufficientlynarrow to exclude a non-negligible difference, given that the treatments are trulyequivalent. The choice of “non-negligible” difference requires justification, and may besmaller than the minimal clinically relevant difference referred to above in the context oftrials designed to establish that a difference exists. In bioequivalence trials the use of a 90%confidence interval is conventional; therapeutic clinical trials may require the use ofconfidence intervals with greater coverage probability (e.g. 95%) in order to achievesufficient impact.

The sample size in a group sequential trial cannot be fixed in advance because it dependsupon the play of chance in combination with the chosen stopping rule and the true treatmentdifference. The design of the stopping rule should take into account the consequentdistribution of the sample size, usually embodied in the expected and maximum samplesizes.

6. THE POPULATIONIn the earlier phases of product development the choice of patients for a clinical trial may beheavily influenced by the wish to maximise the chance of observing specific clinical effects

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of interest, and hence they may come from a very narrow sub-group of the total patientpopulation for which the substance may eventually be indicated. However by the time thepivotal Phase III trials are undertaken, the patient populations should more closely mirrorthe intended users. Hence in these trials it is generally helpful to relax the inclusion andexclusion as much as possible within the target indication, whilst maintaining sufficienthomogeneity to permit a successful trial to be carried out. No individual clinical trial can beexpected to be totally representative of future users, because of the possible influences of thegeographical location, the time when it is conducted, the medical practices of the particularinvestigator(s) and clinics, and so on. However the influence of such factors should bereduced wherever possible, and subsequently discussed during the interpretation of the trialresults.

It is unusual for all eligible patients considered for entry to a trial to be included. In pivotaltrials, it is recommended that a log should be kept of all screened patients so as to allowsome assessment of the numbers and characteristics of the excluded patients, and thereasons for their exclusion.

7. DESIGN TECHNIQUES TO AVOID BIASThe two most important design techniques for avoiding bias in clinical trials are blindingand randomisation, and these should be a normal feature of most controlled clinical trialsintended to be included in the regulatory application for a new product. Most such trialsfollow a double-blind approach in which treatments are pre-packed in accordance with asuitable randomisation schedule, and supplied to the trial centre(s) labelled only with thepatient number and the treatment period so that no-one involved in the conduct of the trial i saware of the specific treatment allocated to any particular patient, not even as a code letter.This approach will be assumed in Sections 7.1 and most of Section 7.2, exceptions beingconsidered at the end.

7.1 Blinding

Blinding is intended to limit the occurrence of conscious and unconscious bias in theconduct and interpretation of a clinical trial arising from the influence which theknowledge of treatment may have on the recruitment and allocation of patients, theirsubsequent care, the attitudes of patients to the treatments, the assessment of end points, thehandling of withdrawals, the exclusion of data from analysis, and so on. The essential a imis to prevent identification of the treatments until all such opportunities for bias are passed.

In a double-blind trial neither the patient nor any of the staff involved in the treatment orclinical evaluation of the patient is aware of the treatment received. In a single blind trialthe investigator and/or his staff are aware of the treatment but not the patient. In an open-label trial the identity of treatment is known to all. The double-blind trial is the optimalapproach. This requires that the treatments to be applied during the trial cannot bedistinguished in any way (appearance, taste, etc.) either before or during administration.

Difficulties in achieving the double-blind ideal can arise: the treatments may be of acompletely different nature – for example, surgery and medicinal product therapy; twosubstances may have different galenic forms and, although they could be madeindistinguishable by the use of capsules, changing the galenic form might also change thepharmacokinetic and/or pharmacodynamic properties and hence require that bioequivalence

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of the forms be established; the daily pattern of administration of two treatments may differ.One way of achieving double-blind conditions under these circumstances is to use a doubledummy technique. This technique may sometimes force an administration scheme which issufficiently unusual to influence adversely the motivation and compliance of the patients.Ethical difficulties may also interfere with its use when, for example, it entails dummyoperative procedures. Nevertheless extensive efforts must be made to overcome thesedifficulties.

If a double-blind trial is not feasible, then the single blind option should be considered. Insome cases only an open-label trial is practically or ethically possible. Under either of thesecircumstances it is preferable, where possible, for clinical assessments to be made bymedical staff who are not involved in treating the patients and who remain blind totreatment. In single blind or open-label trials every effort should be made to minimise thevarious known sources of bias. The reasons for the degree of blinding adopted should beexplained in the protocol, together with steps taken to minimise bias by other means.

Any intentional or unintentional breaking of the blind must be reported at the end of thetrial, irrespective of the reason for its occurrence.

7.2 Randomisation

Randomisation introduces a deliberate element of chance into the assignment of treatmentsto patients in a clinical trial. During subsequent analysis of the trial data, it provides asound statistical basis for the quantitative evaluation of the evidence relating to treatmenteffects. It also tends to produce treatment groups in which the distributions of prognosticfactors (known and unknown) are similar. In combination with blinding, randomisationhelps to avoid possible bias in the selection and allocation of patients arising from thepredictability of treatment assignments.

The randomisation schedule of a clinical trial documents the random allocation oftreatments to patients. In the simplest situation it is a sequential list of treatments (ortreatment sequences in a cross-over study) or corresponding codes by patient number. Thelogistics of some studies, such as those with a screening phase, may make matters morecomplicated, but the unique pre-planned assignment of treatment, or treatment sequence, topatient should be clear. Different designs of study will require different procedures forgenerating randomisation schedules. This procedure should be capable of being reproduced(if the need arises) through the use of the same random number table, or the same computerroutine and seed for its random number generator.

Although unrestricted randomisation is an acceptable approach, some advantages cangenerally be gained by randomising patients in blocks. This helps to increase thecomparability of the treatment groups particularly when patient characteristics may changeover time, as a result, for example, of changes in recruitment policy. It also provides a betterguarantee that the treatment groups will be of nearly equal size. In cross-over trials itprovides the means of obtaining balanced designs with their greater efficiency and easierinterpretation. Care must be taken to choose block lengths which are sufficiently short tolimit possible imbalance, but which are long enough to avoid predictability towards the endof the sequence in a block. Investigators should generally be blind to the block length; the useof two or more block lengths, randomly selected for each block, can achieve the samepurpose. (Strictly, in a double-blind trial predictability does not matter, but thepharmacological effects of medicinal products often provide the opportunity for intelligentguesswork.)

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In multicentre studies the randomisation procedures should always be organised centrally.It is advisable to have a separate random scheme for each centre i.e. to stratify by centre.More generally, stratification by important prognostic factors measured at baseline (e.g.severity of disease, age, sex, etc.) may sometimes be valuable in order to promote balancedallocation within strata; this has greater potential benefit in small trials. The use of morethan two or three stratification factors is rarely necessary, is less successful at achievingbalance and is logistically troublesome. Where it is necessary the use of a dynamicallocation procedure (see below) may help to achieve balance across all factorssimultaneously provided the rest of the trial procedures can be adjusted to accommodate anapproach of this type.

The next patient to be randomised into a study should always receive the treatmentcorresponding to the next free number in the appropriate randomisation schedule (in therespective stratum, if randomisation is stratified). The appropriate number and associatedtreatment pack for the next patient should only be allocated when entry of that patient to therandomised part of the trial has been confirmed. These tasks will normally be carried outby staff at the investigator’s centre, who will then dispense the relevant blinded trialsupplies. Details of the randomisation which facilitate predictability (e.g. block length)should not be contained in the main study protocol, but should be set out in an addendumwhich can be withheld from the study sites. The randomisation schedule itself should befiled securely by the applicant in a manner which ensures that blindness is properlymaintained throughout the trial. Access to the randomisation schedule during the trial musttake into account the possibility that, in an emergency, the blind may have to be broken forany patient, either partially or completely. The procedure to be followed, the necessarydocumentation, and the subsequent treatment and assessment of the patient should all bedescribed in the protocol.

Alternative randomisation procedures generally require some relaxation of the degree ofblindness. An important case is when the treatment code of each patient is known althoughthe assignment of actual treatment to treatment codes is not; this is still technically double-blind but the groups of patients on a common treatment are identifiable. This relaxation isnecessary to permit the normal methods of dynamic allocation to be used. In these, theallocation of treatment to a patient may be influenced by the current balance of allocatedtreatments and, in a stratified trial, by the stratum to which the patient belongs and thebalance within each prognostic factor. Knowledge of the treatment code may be restricted to acentral trial office from where the dynamic allocation is controlled, generally throughtelephone contact. This in turn permits additional checks of eligibility criteria andestablishes entry into the trial – these features can be valuable in certain types of multicentretrial. The usual system of pre-packing and labelling product supplies for double-blind trialscan then be followed, but the order of their use is no longer sequential. (It is even possiblethrough the use of appropriate computer algorithms to keep the personnel at the central trialoffice blind to the treatment code.)

Single blind and open-label trials provide additional flexibility, but in these it i sparticularly important to take care that the investigator’s knowledge of the next treatmentdoes not influence his decision to enter the patient as randomised: his decision shouldalways precede knowledge of the randomised treatment. Any decision to reduce the level ofblinding in order to use a particular method of randomisation requires careful justification.

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8. PRIMARY AND SECONDARY VARIABLESThe primary variable (‘target’ variable, primary endpoint) should be the variable capable ofproviding the most relevant and convincing evidence directly related to the primaryobjective of the trial. There should generally be only one primary variable and this willusually be an efficacy criterion, because the primary objective of most confirmatory trialsconcerns efficacy. The selection of the primary variable must reflect the accepted norms andstandards in the relevant field of research. The use of a reliable and validated variable withwhich experience has been gained either in earlier studies or in published literature i srecommended. There should be sufficient evidence that the primary variable will besensitive to clinically relevant treatment effects in the patient population described by theinclusion and exclusion criteria.

The primary variable should be specified in the protocol. A post-hoc definition will rarely beacceptable, since the biases this introduces are difficult to assess. When the clinical effectdefined by the primary objective is to be measured in more than one way, then the protocolshould identify one of the measurements as the primary variable, whenever possible. If thisis not possible, another useful strategy is to combine the multiple measurements into asingle variable, perhaps with suitable weighting; indeed, the primary variable sometimesarises naturally as a combination of multiple clinical measurements (e.g. the rating scalesused in arthritis, psychiatric disorders and elsewhere). In either case, the method ofcombining the multiple measurements should be specified in the protocol, and aninterpretation of the new scale should be provided in terms of the size of a clinically relevantbenefit. The primary variable is also the most appropriate one to use in the protocol forestimating the sample size (see section 5).

It may sometimes be desirable to use more than one primary variable to cover the range ofeffects of the therapies, simultaneous evidence of effect on each of them (or a pre specifiedsubset of them) being sought in order to demonstrate efficacy of the product. The plannedmanner of interpretation of this type of evidence must be carefully spelled out and the effecton the type I error explained, because of the potential for multiple comparison problems (seeSection 10.5).

When direct measurement of the clinical benefit to the patient is not feasible, indirectcriteria (so-called surrogate variables) may have to be considered. The use of a surrogatevariable as a primary variable requires careful justification of the claim that, under thecircumstances of the trial, the anticipated or observed treatment effects on the surrogatevariable predict clinical benefits of value to the patient.

Secondary variables are either supportive measurements related to the primary objective ormeasurements of effects related to the secondary objectives. Their pre-definition in theprotocol is also important.

On some occasions categorisation or dichotomisation of continuous or ordinal variablesmay be necessary in which case the criteria should be specified in advance in the protocol.Criteria of success and response are common examples of dichotomies which require precisespecification in terms of, for example, a minimum percentage improvement (relative tobaseline) in a continuous variable, or a ranking categorised as a minimum of ‘good’ on anordinal rating scale.

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9. THE CASE REPORT FORMThe form and the content of the case report forms (CRFs) must be in full accordance with theprotocol and must be established in advance of the conduct of the study. Case report formsshould only include relevant items which will be evaluated in the final report. Data fieldsshould be designed so that “missing values” can be distinguished from “value zero” or“characteristic absent”. Verbal scales should be exhaustive and overlapping categoriesshould be avoided so that unambiguous answers are obtained. It is generally moreappropriate to document the absolute value on a rating scale rather than changes from abaseline. If changes are documented, then the time point to which the change is relatedshould be made clear and unambiguous.

The CRF should be filled out during the course of the trial and the dates to which the dataapply and on which the form was completed should be noted. Subsequent additions oramendments to the form should be avoided, except as a means of correcting errors identifiedbefore analysis during a planned process of monitoring or quality control, in which case thechanges should be properly documented, signed and dated.

Similar considerations apply to data collected via a medium other than paper, such as theelectronic medium employed in remote data entry. Further guidance relating to CRFs can befound in Chapter 3 of GCP.

10. PRE SPECIFIED DATA ANALYSISWhen designing a clinical trial, it is good practice to consider the eventual analysis of thedata and to document the resulting plans – the “analysis plan”. In the case of an exploratorytrial the plan may describe only general principles and directions, but in a confirmatorytrial the plan should be precise in a number of respects if the credibility of the findings is tobe maximised. All features of the proposed confirmatory analysis of the primary variable(s),including the way in which anticipated analysis problems will be handled, should becovered in the plan normally within the protocol. The principal features of the analysis ofall other data should also be outlined.

It is also valuable to review the analysis plan when the study data are complete andavailable for review but whilst the statistician (amongst others) is still blinded to treatment,and hence before the main analysis. This will be referred to as the “blind review”.

10.1 Study populations

The analysis plan should first define the population of patients whose data it is planned toinclude in the main analyses. In addition in pivotal trials any available data on the widerpopulation screened for entry, or enrolled into a screening phase of the study prior torandomisation, should be summarised within the bounds (if any) imposed by the need forinformed consent. The intention of this planned summary is to provide information aboutthe numbers and characteristics of excluded patients, both eligible and ineligible, togetherwith their reasons for exclusion, in order to guide assessment of the potential practicalimpact of the study results. As a minimum, documentation is required for all patients forwhom study procedures were initiated and who have given their informed consent. Thecontent of this patient documentation depends on detailed features of the particular trial, butat least demographic and baseline data on disease status should be collected wheneverpossible.

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If all patients randomised into a clinical trial satisfied all entry criteria, followed all trialprocedures perfectly with no losses to follow up, and provided complete data records, then thepopulation of patients to be included in the analysis would be self-evident. The design andconduct of a trial should aim to approach this ideal as closely as possible but, in practice, it isdoubtful if it can ever be fully achieved, and hence the analysis plan should address anyanticipated problems prospectively in terms of how these affect the patients and data to beanalysed. Decisions concerning the analysis population should be guided by the principlesunderlying the “intention-to-treat” and the “per protocol” strategies.

10.1.1 The intention-to-treat population

The principle of intention-to-treat (ITT) implies that all randomised patients should beincluded in the analysis. In most clinical trials it provides a conservative approach, andalso gives estimates of treatment effects which are more likely to mirror those observed i nsubsequent practice. In practice the protocol should try to avoid or ameliorate each type ofirregularity which is anticipated during the trial and which might impair a satisfactoryITT analysis. Wherever possible, it should also define prospectively how any unavoidableproblems will be addressed. Any objective entry criteria, measured before randomisation,which will be used to exclude patients from analysis should be pre-specified and justified, forexample, those relating to the presence or absence of the disease under investigation. Anyother anticipated reasons for excluding patients from ITT analysis should be justified.

The problems associated with ITT lie in the handling of some irregularities (incorrectlyentered patients, errors in treatment assignment, missing data, loss to follow up, and someother protocol violations) and the subtleties which this can involve. For example, patientswho fail to satisfy an objective entry criterion measured prior to randomisation, but whoerroneously enter the trial, may be excluded from analysis without introducing bias into thetreatment comparison. However not all incorrectly entered patients fall into this category.As another example, patients withdrawn from treatment may introduce serious bias and, i fthey have provided no data after withdrawal, ITT offers no obvious solution. The necessaryinclusion of such patients in the analysis may require some re-definition of the primaryvariable, or some assumptions about the patients’ fate.

Measurements of primary variables made at the time of withdrawal (or at the time of theloss of the patient for any other reason), or subsequently collected in accordance with theprotocol, are valuable in the context of ITT analysis. Their use in analysis should bedescribed and justified in the analysis plan and their collection described elsewhere in theprotocol. However, the use of techniques such as “last observation carried forward” (LOCF)should recognise the fact that it can lead to biased estimates of treatment effects when thelikelihood of the loss of a patient is related to treatment or response. Any other methods to beemployed to ensure the availability of measurements of the primary variable for everypatient in the ITT analysis should be described.

Because of the complexity of the problems connected with ITT it may sometimes be preferableto defer detailed consideration of the manner of dealing with irregularities until the blindreview of the data at the end of the study and, if so, this should be stated in the analysis plan.

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10.1.2 The per protocol population

The ‘per protocol’ population, sometimes described as the ‘valid cases’, the ‘efficacy’population or the ‘evaluable patient’ population, is a subset of the intention-to-treat populationand is characterised by the following criteria:

• the completion of a certain pre-specified minimal exposure to the treatment regimen,

• the availability of measurements of the primary variable(s) at relevant andpre-specified time(s),

• the absence of any major protocol violation including the violation of entry criteria(where the nature of and reasons for these protocol violations must be defined anddocumented before breaking the blind).

This population generally maximises the opportunity for a new treatment to show additionalefficacy in analysis, and most closely reflects the scientific model underlying the protocol.However it is not conservative, and is more vulnerable to biases than ITT.

10.1.3 The roles of the intention-to-treat and the per protocol analyses

In general, it is advantageous to demonstrate a lack of sensitivity of the principal trialresults to alternative choices of patient population for analysis. In pivotal trials it is usuallyappropriate to plan to conduct both ITT and per protocol analyses, so that any differencesbetween them can be the subject of explicit discussion and interpretation subsequently. Insome cases, it may be desirable to plan further exploration of the sensitivity of conclusions tothe choice of population analysed. When the ITT and the per protocol analyses come toessentially the same conclusions, confidence in the study results is increased, bearing i nmind, however, that the need to exclude a substantial proportion of the ITT population fromthe per protocol analysis throws some doubt on the overall validity of the study.

ITT and per-protocol analyses play different roles in comparative trials (which seek to showone active substance to be superior), and in equivalence trials (which seek to showmedicinal products to be similar – see Section 4.3). In comparative studies the ITT analysisusually tends to avoid the optimistic estimate of efficacy which may result from a perprotocol analysis, since the noncompliers included in an ITT analysis will generallydiminish the overall treatment effect. However in an equivalence trial ITT no longerprovides a conservative strategy and its role should be considered very carefully. Hence i ncomparative trials, particularly those claiming to be pivotal with regard to efficacy, the ITTanalysis will normally be of higher priority, whereas in equivalence trials this is not thecase.

10.2 Missing values and outliers.

Missing values represent a potential source of bias in a clinical trial. Hence, every effortshould be undertaken to fulfil all the requirements of the protocol concerning the collectionof data and their subsequent management. However, in reality there will almost always besome missing data. A study may be regarded as valid, none-the-less, provided the methods ofdealing with missing values are sensible, and particularly if those methods are pre-definedin the analysis plan of the protocol. Pre-definition of methods may be facilitated by updatingthis aspect of the analysis plan during the blind review. Unfortunately, no universallyapplicable methods of handling missing values can be recommended. An investigation

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should be made concerning the sensitivity of the results of analysis to the method ofhandling missing values, especially if the number of missing values is substantial.

A similar approach should be adopted to exploring the influence of outliers, the statisticaldefinition of which is, to some extent, arbitrary. Clear identification of a particular value asan outlier is most convincing when justified medically as well as statistically, and themedical context will then often define the appropriate action. Any outlier procedure set out i nthe protocol should be such as not to favour any treatment group a priori. Once again, thisaspect of the analysis plan can be usefully updated during blind review. If no procedure fordealing with outliers was foreseen in the study protocol, one analysis with the actual valuesand at least one other analysis eliminating or reducing the outlier effect should beperformed and differences between their results discussed.

10.3 Data transformation/modification

The decision to transform key variables prior to analysis is best made during the design ofthe trial on the basis of similar data from earlier clinical trials. Transformations (e.g.square root, logarithm) should be specified in the protocol and a rationale provided,especially for the primary variable(s). The general principles guiding the use oftransformations are to be found in standard texts; conventions for particular variables havebeen developed in a number of specific clinical areas. The decision on whether and how totransform a variable should be influenced by the preference for a scale which facilitatesclinical interpretation.

Similar considerations apply to other data modifications sometimes used to create a keyvariable for analysis, such as the use of change from baseline, percentage change frombaseline, the ‘area under the curve’ of repeated measures, or the ratio of two differentvariables. Subsequent clinical interpretation should be carefully considered, and themodification should be justified in the protocol. Closely related points are made in Section 8.

10.4 Estimation, confidence intervals and hypothesis testing.

The statistical analysis plan should specify the hypotheses which are to be tested and/or thetreatment effects which are to be estimated in order to satisfy the objectives of the trial. Thestatistical methods to be used to accomplish these tasks should be described for the primary(and preferably the secondary) variables, and the underlying statistical model should bemade clear. Estimates of treatment effects should be accompanied by confidence intervals,whenever possible, and the way in which these will be calculated should be identified. Theplan should also describe any intentions to use baseline data to improve precision and toadjust estimates for potential baseline differences, for example by means of analysis ofcovariance. The reporting of precise numerical probabilities (e.g.”P=0.034”) should beenvisaged in the plan, rather than exclusive reference to critical values (e.g. “P<0.05”). It i simportant to clarify whether one- or two-sided tests of statistical significance will be used,and in particular to justify prospectively the use of one-sided tests. If formal hypothesis testsare not considered appropriate, then the alternative process for arriving at statisticalconclusions should be given.

The particular statistical model chosen should reflect the current state of the art. All effectsto be fitted in the analysis (for example in analysis of variance models) should be fullyspecified, and the manner, if any, in which this set of effects might be modified in responseto preliminary results should be explained. The same considerations apply to the set of

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covariates fitted in an analysis of covariance. (See also Section 10.6). Due attention shouldbe paid to the statistical distribution of both primary and secondary variables. The pre-planned use of non-parametric methods to avoid distribution difficulties is acceptable. Whenmaking this choice it is important to bear in mind the need to provide statistical estimates ofthe size of treatment effects, together with confidence intervals, as this may influence thechoice of method in cases of doubt. Any essential changes to the pre-planned statisticalmodelling procedure should be made during blind review.

The analysis of the primary variable by which the primary objective of the trial will bejudged must be clearly distinguished from supporting analyses of the primary or secondaryvariables. In these other analyses, the number of significance tests should be minimisedand preference given to descriptive methods and estimation procedures whenever possible.Within the analysis plan there should also be an outline of the way in which data other thanthe primary and secondary variables will be summarised and reported. This should includea reference to any approaches adopted for the purpose of achieving consistency of analysisacross a range of studies, for example for safety data.

10.5 Adjustment of type I error

When multiplicity is present, the usual frequentist approach to the analysis of clinical trialdata may require an adjustment to the type I error. Multiplicity may arise from multipleprimary variables (see Section 8), multiple comparisons of treatments, repeated evaluationover time and/or interim analyses (see Section 11.4). Methods to avoid or reduce multiplicityare sometimes preferable when available, such as the identification of the key primaryvariable (multiple variables), the choice of a critical treatment contrast (multiplecomparisons), the use of a summary measure such as “area under the curve” (repeatedmeasures), and the use of extreme type I errors (interim analysis). In confirmatoryanalyses, any aspects of multiplicity which remain after steps of this kind have been takenshould be identified in the protocol; adjustment should always be considered and the detailsof any adjustment procedure should be set out in the analysis plan.

10.6 Subgroups, interactions and covariates

The primary variable(s) is often systematically related to other influences apart fromtreatment. For example, there may be relationships to covariates such as age and sex, orthere may be differences between specific subgroups of patients such as those treated at thedifferent centres of a multicentre trial. In some instances an adjustment for the influence ofcovariates or for subgroup effects is an integral part of the analysis plan and hence shouldbe set out in the protocol. Pre-study deliberations should identify those covariates and factorsexpected to have an important influence on the primary variable(s), and should considerhow to account for these in the analysis in order to improve precision and to compensate forany lack of balance between treatment groups. When the potential value of an adjustment i sin doubt, it is often advisable to nominate the unadjusted analysis as the one for primaryattention, the adjusted analysis being supportive. Special attention should be paid to centreeffects and to the role of baseline measurements of the primary variable. It is not advisableto adjust the main analyses for covariates measured after randomisation.

The treatment effect itself may also vary with subgroup or covariate – for example, the effectmay decrease with age or may be larger in a particular diagnostic category of patient. Insome cases such interactions are anticipated, and hence a subgroup analysis, or a statisticalmodel including interactions, is part of the confirmatory analysis plan. In most cases,

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however, subgroup or interaction analyses are exploratory and should be clearly identifiedas such; they should explore the uniformity of any treatment effects found overall. Ingeneral, such analyses should proceed through the addition of interaction terms to thestatistical model in question, rather than through multiple separate analyses within eachsubgroup of patients, or within strata defined by the covariates. When exploratory, theseanalyses should be carried out informally and interpreted cautiously; any claims oftreatment efficacy based solely on exploratory subgroup analyses are unlikely to be accepted.

11. THE CONDUCT AND MONITORING PHASECareful conduct of a trial according to the protocol has a major impact on the credibility ofthe study results. Careful monitoring can ensure that difficulties are noticed early and theirrecurrence minimised. Both help to permit a straightforward and unambiguous analysis.The period of conduct and monitoring starts with the selection of the study sites and endswith the collection and cleaning of the last patient’s data. In some cases, employees of thesponsor may suffice to monitor the quality of the trial activities and data, while in othercases an independent and experienced body of specialists (a monitoring committee) willalso be required. The latter is appropriate if formal interim analyses are planned, withsome lifting of the blindness being necessary, and/or if regular and independent reviews ofsafety are required. The employees of the sponsor and the monitoring committee both requireaccess to statistical expertise for advice and assistance. This may relate to the handling ofunexpected protocol violations to minimise effects on the analysis (sponsor), or to theexecution, interpretation or modification of interim analyses (monitoring committee).

11.1 Changes in inclusion and exclusion criteria

Inclusion and exclusion criteria should, if possible, remain constant, as specified in theprotocol, throughout the period of patient recruitment. However, occasionally this may notprove possible; in long-term studies, for example, growing medical knowledge either fromoutside the trial or from interim analyses may suggest a change of entry criteria. Changesmay also result from the discovery by monitoring staff that regular violations of the entrycriteria are occurring, or that seriously low recruitment rates are due to over-restrictivecriteria. The protocol amendment implementing such changes should cover any statisticalconsequences, such as sample size adjustments arising from different event rates, ormodifications to the analysis plan.

11.2 Accrual rates

In studies with an appreciable time-scale for the accrual of patients, the rate of accrualshould be monitored and, if it falls appreciably below the projected level, the reasons shouldbe identified and remedial actions taken in order to protect the power of the trial and allayconcerns about selective entry.

In a multicentre trial the accrual rate of patients at the various study sites should also bemonitored to seek to ensure that the centres do not diverge excessively in the numbers ofpatients entered (see Section 4.1).

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11.3 Checking the design assumptions

In large trials there will usually be an opportunity to check the assumptions which underlaythe original design and sample size calculations. This may be particularly important if thetrial specifications have been made on preliminary and/or uncertain information. A ninterim check conducted on the blinded data may reveal that overall response variances,event rates or survival experience are not as anticipated. A revised sample size may then becalculated using suitably modified assumptions, and should be justified and documented i na protocol amendment and in the final report. The steps taken to preserve blindness and theconsequences, if any, for the type I error and the width of confidence intervals should beexplained. The potential need for re-estimation of the sample size should be envisaged in theprotocol whenever possible (see Section 5).

Substantial differences between the anticipated and observed average level of the primaryvariable(s) may pose additional design problems for a trial, because it may alter judgementconcerning the treatment difference to be detected, or the size of the non-negligible differenceto be excluded in the case of an equivalence trial. In addition, the validity of an equivalencetrial is judged by its similarity to earlier trials of the positive control, and substantialdifferences in the level of the primary variable do not support the idea of similarity.

11.4 Interim analyses and early stopping

When interim analysis is planned, this is usually accomplished by the use of a groupsequential design (see Section 4.5). The goal of such an interim analysis is to stop the trialearly if the superiority of the treatment under test is already clearly established, if thedemonstration of a relevant treatment difference has become unlikely, or if unacceptableadverse effects are apparent. The schedule of analyses, or at least the considerations whichwill govern its generation, should be stated in the protocol or appended to it before the time ofthe first interim analysis; the stopping rules and their properties should also be clearlystated there. This material should be written or approved by the monitoring committee, whenthe study has one. Deviations from the planned procedure always bear the potential ofinvalidating the study results. If it becomes necessary to make changes to the trial, anyconsequent amendments to the statistical procedures should be specified in the protocol at theearliest opportunity. The procedures selected should always ensure that the overall type Ierror is, at least, maintained.

The execution of an interim analysis must be a completely confidential process becauseunblinded data and results are potentially involved. All staff involved in the conduct of thetrial should remain blind to the results of such analyses, because of the possibility that theirattitudes to the trial will be modified and cause changes in recruitment patterns or biases i ntreatment comparisons. This applies equally to the investigators and their staff and to staffemployed by the applicant. Investigators should only be informed about the decision tocontinue or to discontinue the trial.

Any interim analysis planned for administrative purposes only, with no adjustment of thetype I error, should also be described in the protocol and subsequently reported. The purposesof an analysis of this type should be clearly stated, and should specifically exclude anypossibility of early stopping or other major changes in design. The blind should not bebroken.

Any unplanned or incorrect interim analysis (with or without the consequence of stoppingthe trial early) can flaw the results of a trial, and weaken confidence in the conclusions

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drawn. Such analyses should therefore be avoided if at all possible. If an unplanned interimanalysis cannot be avoided, the study report must later explain carefully why it wasnecessary, the degree to which blindness had to be lifted, and what resulting actions werepossible in principle.

12. INTEGRITY OF DATA AND COMPUTER SOFTWAREThe credibility of the numerical results of the analysis depends on the quality and validityof the methods and software used both for data management (data entry, storage,verification, correction and retrieval) and also for processing the data statistically. Datamanagement activities must therefore be based on thorough and effective standard operatingprocedures (SOPs). The computer software used for data management and statisticalanalysis must be completely reliable, and documentation of appropriate validationprocedures should be available. The computer systems and packages to be used shouldpreferably be identified in the protocol.

13. EVALUATION AND REPORTINGAs stated in the Introduction, the structure and content of clinical reports is the subject ofanother note for guidance on Structure and Content of Clinical Study Reports. This note forguidance fully covers the reporting of statistical work, appropriately integrated with clinicaland other material. The current section is therefore relatively brief.

During the planning phase of a trial the main features of the analysis should have beenspecified in an analysis plan and included in the protocol as described in Section 10. Whenthe conduct of the trial is over and the data are assembled and available for preliminaryinspection, it is valuable to carry out the blind review of the planned analysis also describedin Section 10. This pre-analysis review, blinded to treatment, should cover decisionsconcerning the exclusion of patients or data from the analysis population(s); possibletransformations may also be checked, and outliers defined; important covariates identifiedin other recent research may be added to the model; the use of parametric or non-parametricmethods may be reconsidered. Decisions made at this time should be described in reports,and should be distinguished from those made after the statistician has had access to thetreatment codes, as blind decisions will generally carry greater weight.

Many of the more detailed aspects of presentation and tabulation, particularly of the lesscritical data, may be finalised at or about the time of the blind review so that by the time ofthe actual analysis full plans exist for all its aspects including patient selection, dataselection and modification, data summary and tabulation, estimation and hypothesistesting. Once data validation is complete, the analysis should proceed according to the pre-defined plans; the more these plans are adhered to, the greater the credibility of the results.Particular attention should be paid to any differences between the planned analysis and theactual analysis, and a careful explanation should be provided.

All patients who entered the trial should be accounted for in the report, whether or not theyare part of an analysis population. All reasons for exclusion from analysis should bedocumented; for any patient included in the intention-to-treat population but not in theper-protocol population, the reasons for exclusion from the latter must also be documented.Similarly, for all patients included in an analysis population, the measurements of al l

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important variables should be accounted for at all relevant time-points. Further availableinformation on additional patients screened for entry but not randomised should also besummarised (see Section 10.1).

The effect of all losses of patients or data, withdrawals from treatment and major protocolviolations on the main analyses of the primary variable(s) should be considered carefully.Patients lost to follow up or withdrawn from treatment should be identified, and a descriptiveanalysis of them provided, including the reasons for their loss and its relationship totreatment and outcome.

Descriptive statistics form an indispensable part of reports. Suitable tables and/or graphicalpresentations should illustrate clearly the important features of the primary and secondaryvariables and of key prognostic and demographic variables. The results of the mainanalyses relating to the objectives of the trial should be the subject of particularly carefuldescriptive presentation.

Although the primary goal of the analysis of a clinical trial should be to answer thequestions posed by its main objectives, new questions based on the observed data may wellemerge during the unblinded analysis. Additional and perhaps complex statistical analysismay be the consequence. This additional work should be strictly distinguished in the reportfrom work which was planned in the protocol.

The play of chance may lead to unforeseen imbalances between the treatment groups i nterms of baseline measurements not pre-defined as covariates in the analysis plan buthaving some prognostic importance nevertheless. This is best dealt with by showing that asubsidiary analysis which accounts for these imbalances reaches essentially the sameconclusions as the planned analysis. If this is not the case, the effect of the imbalances onthe conclusions should be quantified.

In general, sparing use should be made of unplanned subsidiary analyses. Subsidiaryanalyses are often carried out when it is thought that the treatment effect may varyaccording to some other factor or factors. An attempt may then be made to identify subgroupsof patients for whom the effect is particularly beneficial. The potential dangers ofover-interpretation of unplanned subgroup analyses are well known (see also Section 10.4),and should be carefully avoided. Although similar problems of interpretation arise if atreatment appears to have no benefit, or an adverse effect, in a subgroup of patients, suchpossibilities must be properly assessed and should therefore always be reported.

Finally statistical judgement should always be brought to bear on the analysis,interpretation and presentation of the results of a clinical trial. To this end the trialstatistician should be a member of the team responsible for the study report, and should be asignatory to it.

14. OUTLINE OF SAFETY ISSUESControlled clinical trials are rarely sufficiently powerful to detect infrequent adverse effectsof treatments. Nevertheless, it is important to monitor Phase III clinical trials for thoseadverse effects which do become apparent. Few Phase III clinical trials nominate a safetyvariable as a primary variable in the protocol but, if claims of superior safety or toleranceare made for a product, they should, in general, be supported by relevant evidence i nconfirmatory studies.

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In any clinical trial the methods and measurements chosen to establish the safety of asubstance will depend on a number of factors, including knowledge of the adverse effects ofclosely related substances, information from pre clinical and earlier clinical studies, andpossible consequences of the pharmacodynamic/ pharmacokinetic properties of the particularproduct, the mode of administration, the type of patients to be studied, and the duration of thestudy. Laboratory variables, vital signs, and adverse events form the main body of the safetydata.

For the purposes of overall safety assessment, the study population is usually defined asthose patients who received at least one dose of the product. Safety variables shouldsubsequently be collected as comprehensively as possible from these patients, whatever theirfate. Additional safety analyses may be required in specific sub populations, such as theelderly, the severely ill, or those who have a common concomitant treatment. Theseanalyses may need to address more specific safety issues.

All safety variables will require attention during analysis, and the broad approach shouldbe indicated in the protocol. All available data in the study population should be included i nthe analysis. All adverse events should be reported, whether or not they are considered to berelated to treatment. Definitions of measurement units and reference ranges of laboratoryvariables should be made with care; if different units or different reference ranges appearin the same trial (e.g. if more than one laboratory is involved), then measurements shouldbe appropriately standardised to allow a unified analysis.

The investigation of safety and tolerability is a multi-dimensional problem. Although somespecific adverse effects of any substance can usually be anticipated and specificallymonitored, the range of possible adverse effects is very large, and new and unforeseeablereactions are always possible. This background underlies the statistical difficultiesassociated with the analytical evaluation of safety and tolerability of products, and meansthat confirmatory information from Phase III clinical trials is the exception rather than therule in the safety field. In most trials the safety implications are best addressed by applyingdescriptive statistics to the safety data, supplemented by confidence intervals wherever thisaids interpretation. Hypothesis tests are sometimes useful either as an aid to evaluating aspecific difference of interest, or as a "flagging" device applied to a large number of safetyvariables to highlight differences worth further attention. If hypothesis tests are used,statistical adjustments for multiplicity to maintain the type I error are usuallyinappropriate, because the type II error is of more concern. In the majority of studiesinvestigators are seeking to establish that there are no notable differences in safetycompared with either a comparator substance or a placebo and, in principle, a f irmconclusion that no differences exists cannot be drawn from the failure to demonstrate themthrough hypothesis tests. The low power attached to most safety variable comparisonsexacerbates this problem. These considerations, which are similar to those which apply toequivalence trials, generally favour the use of confidence intervals in preference tohypothesis tests for the analysis of safety data.

For more details of the reporting requirements relating to safety see Chapter 12 of the note forguidance on Structure and Content of Clinical Study Reports.

15. SUMMARISING THE CLINICAL DATABASERegulatory review inevitably involves the summary and synthesis of the evidence on safetyand efficacy from all the reported clinical trials. When carrying out this task, applicants

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should conform to the requirements of the relevant section of the Notice to Applicants. A noverall summary may be accompanied by a formal meta-analysis, if appropriate.

Within the summary a number of areas of specific statistical interest arise: describing thedemography and clinical features of the population treated during the course of the clinicaltrial programme; addressing the key questions of efficacy by considering the results of therelevant (usually controlled) trials and highlighting the degree to which they reinforce orcontradict each other; working up the safety information which is available from thecombined database of all the studies whose results contribute to the marketing authorisationapplication and identifying potential safety issues. During the design of a clinicalprogramme careful attention should be paid to the uniform definition and collection ofmeasurements which will facilitate subsequent interpretation of the series of trials,particularly if they are likely to be combined across trials. A common dictionary forrecording the details of medication, medical history and adverse events should be selectedand used. A common definition of the primary and secondary variables is nearly alwaysworthwhile, and essential for meta-analysis. The manner of measuring key efficacyvariables, the timing of assessments relative to randomisation/entry, the handling ofprotocol violators and deviators, and perhaps the definition of prognostic factors, should al lbe kept compatible unless there are compelling reasons not to do so, at least in the pivotalstudies.

Any statistical procedures used to combine data across trials must be described in detail.Attention should be paid to the possibility of bias associated with the selection of trials, to thehomogeneity of their results, and to the proper modelling of the various sources of variation.The sensitivity of conclusions to the assumptions and selections made should be explored.

15.1 Efficacy data

Individual clinical trials should always be large enough to satisfy their objectives.Additional valuable information may also be gained by summarising a series of clinicaltrials which address essentially identical key efficacy questions. The main results of such aset of studies should always be presented in an identical form to permit comparison, usuallyin tables or graphs which focus on estimates plus confidence limits. The use of meta-analytic techniques to combine these estimates is often a useful addition, because it allows amore precise overall estimate of the size of the treatment effects to be generated, and providesa complete and concise summary of the results of the trials. Under exceptionalcircumstances a meta-analytic approach may also be the most appropriate way, or the onlyway, of providing sufficient overall evidence of efficacy via an overall hypothesis test.

15.2 Safety data

In summarising safety data it is important to examine the safety database thoroughly forany indications of potential toxicity, and to follow up any indications by looking for anassociated supportive pattern of observations. The combination of the safety data from allhuman exposure to the product should provide the main source of information, because itslarger sample size provides the best chance of detecting the rarer adverse events and,perhaps, of estimating their approximate incidence. However, incidence data from thisdatabase are difficult to evaluate without a natural comparator group, and data fromcomparative studies are especially valuable in overcoming this difficulty. The results fromstudies which use a common comparator (placebo or specific active comparator) should becombined and presented separately for each comparator providing sufficient data.

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All indications of potential toxicity arising from statistical exploration of the data should bereported. The evaluation of the reality of these potential adverse effects should take accountof the issue of multiplicity arising from the numerous statistical comparisons made. Theevaluation should also make appropriate use of survival analysis methods to exploit thepotential relationship of the incidence of adverse events to duration of exposure and/orfollow-up. The risks associated with identified adverse effects should be appropriatelyquantified to allow a proper assessment of the risk/benefit relationship.