٧ - AIFA Agenzia Italiana del Farmaco
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٧ - AIFA Agenzia Italiana del Farmaco
Ministero della Salute DIREZIONE GENERALE DELLA VALUTAZIONE DEI MEDICINALI E DELLA FARMACOVIGILANZA Sperimentazione Clinica Programma del Workshop rivolto ai biostatistici operanti presso i Comitati etici “Le competenze biostatistiche nell’ambito dei Comitati etici locali” Roma, 18 marzo 2003 Hotel Universo, Via Principe Amedeo 5/b 9.30 Registrazione dei partecipanti 10.00 Introduzione al corso dr. Tomino 10.10 Dalla superiorità alla non-inferiorità: problemi aperti prof. Marubini 10.40 Disegni sequenziali per gruppi prof. Grigoletto 11.10 Aggiustamenti dei livelli di significatività e di confidenza: necessità e opportunità dr. Cesana 11.40 Ruolo di differenti insiemi di pazienti nell’analisi delle sperimentazioni cliniche dr.ssa Bacchieri 12.10 Dibattito generale 13.00 Pausa pranzo 14.30 Costituzione dei gruppi di lavoro su: Organizzazione delle attività formative prof.ssa Marinoni - dr. Raschetti Revisione delle linee guida dr.ssa Menniti Ippolito - dr.ssa Bacchieri Armonizzazione del comportamento dei biostatistici nel contesto decisionale dei Comitati etici prof. Marubini - dr.ssa Patarnello Organizzazione dello scambio informatizzato di commenti e pareri prof. Grigoletto - dr.ssa Rinieri 16.30 Dibattito generale 17.30 Conclusione dei lavori in collaborazione con ISS (Istituto Superiore di Sanità) SISMEC (Società Italiana di Statistica Medica ed Epidemiologia Clinica) http://oss-sper-clin.sanita.it/ Sommario Sperimentazioni Cliniche dei Medicinali: Attualità e prospettive dr. Tomino Dalla superiorità alla non-inferiorità: problemi aperti prof. Marubini Disegni sequenziali per gruppi prof. Grigoletto Aggiustamenti dei livelli di significatività e di confidenza: necessità e opportunità dr. Cesana Riferimenti bibliografici CPMP – Points to consider on multiplicity issues in clinical trials ICH Harmonised Tripartite Guideline – Statistical principles for clinical trials Ruolo di differenti insiemi di pazienti nell’analisi delle sperimentazioni cliniche dr.ssa Bacchieri Gruppi di lavoro Organizzazione delle attività formative prof.ssa Marinoni – dr. Raschetti Revisione delle linee guida dr.ssa Menniti-Ippolito – dr.ssa Bacchieri Armonizzazione del comportamento dei biostatistici nel contesto decisionale dei Comitati etici prof. Marubini – dr.ssa Patarnello Organizzazione dello scambio informatizzato di commenti e pareri prof. Grigoletto – dr.ssa Rinieri a cura di Simona de Gregori e Roberta Coppari Sperimentazioni Cliniche dei Medicinali: Attualità e prospettive dr. Tomino Roma, 18 Marzo 2003 “Le competenze biostatistiche nell’ambito dei CE locali” Carlo Tomino Ministero della Salute Sperimentazioni Cliniche dei Medicinali: Attualità e prospettive Direzione Direzione Generale Generale Valutazione Valutazione Medicinali Medicinali ee Farmacovigilanza Farmacovigilanza Ministero Ministero della della Salute Salute Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Osservatorio Nazionale sulla Sperimentazione Clinica Informazione Rapporto Annuale delle Sperimentazioni Cliniche dei Medicinali (dicembre) ■ Bollettino Sperimentazione clinica dei medicinali (aggiornamenti semestrali) disponibili (italiano / inglese) sul sito: http://oss-sper-clin.sanita.it Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Ministero della Salute ■ Direzione Generale Valutazione Medicinali e Farmacovigilanza Ministero della Salute Sperimentazione Clinica Roma 2003 SC presentate nel 2° Rapporto Annuale N. SC 2000 544 2001 571 I sem 2002 305 Totale 1420 Direzione Generale Valutazione Medicinali e Farmacovigilanza Ministero della Salute Anno Roma 2003 Tipologia delle SC Multicentriche in Italia 42.1% Studi Multicentrici Internazionali 57.9% Ministero della Salute Studi Multicentrici Nazionali Roma 2003 Direzione Generale Valutazione Medicinali e Farmacovigilanza Distribuzione SC in Italia per fase Direzione Generale Valutazione Medicinali e Farmacovigilanza Ministero della Salute Fase III Fase II Fase IV Bioeq/Biod Fase I 55.8% 31.7% 8.2% 3.0% 1.3% Roma 2003 Distribuzione SC in Italia per Fase e per Anno 2001 I Sem 2002 Fase III 61.6% 52.2% 52.5% Fase II 27.8% 33.1% 36.1% Fase IV 7.9% 10.5% 4.6% Bioeq/Biod 1.8% 3.3% 4.3% Fase I 0.9% 0.9% 2.6% Ministero della Salute 2000 Roma 2003 Direzione Generale Valutazione Medicinali e Farmacovigilanza SC per tipo di sponsor Direzione Generale Valutazione Medicinali e Farmacovigilanza 76.7% 7.8% 7.0% 4.1% 2.5% 2.0% Ministero della Salute Azienda farmaceutica IRCCS (pubblico-privato) ASL Associazione scientifica Università Altro Roma 2003 SC in Italia per Gruppo Anatomico Principale Azienda farmaceutica / Sponsor no profit Direzione Generale Valutazione Medicinali e Farmacovigilanza % No profit 63.1 5.4 9.1 3.2 5.0 3.2 3.2 0.9 3.2 0.6 2.8 0.3 Roma 2003 Ministero della Salute Comitati Etici Direzione Generale Valutazione Medicinali e Farmacovigilanza Ministero della Salute Antineoplastici ed immunomodulatori Sistema Nervoso Antimicrobici per uso sistemico App. gastroint. e metabolismo Sistema cardiovascolare Sangue ed organi ematopoietici Sist. muscolo-scheletrico Sist. genito-urinario ed ormoni sessuali Sistema respiratorio Vari Organi di senso Prep. ormonali sistemici (escl. orm. sessuali) Dermatologici Farmaci antiparassitari, insetticidi, repellenti % Az. farm. 21.4 13.0 12.4 10.3 8.5 6.7 6.4 6.3 4.6 3.7 2.4 2.4 1.5 0.3 Roma 2003 Osservatorio Nazionale sulla Sperimentazione Clinica Comitati Etici presenti accreditati = 289 n. CE % sul totale Lombardia Lazio Sicilia Veneto Campania Puglia Emilia Romagna 55 32 27 24 23 19 18 19.0% 11.1% 9.3% 8.3% 8.0% 6.6% 6.2% Altre regioni 91 31.5% Direzione Generale Valutazione Medicinali e Farmacovigilanza Ministero della Salute Regione Roma 2003 Decentramento autorizzativo sui medicinali vengono approvate direttamente dai Comitati Etici Locali” Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Ministero della Salute “Oggi oltre il 95% delle sperimentazioni cliniche Osservatorio Nazionale sulla Sperimentazione Clinica Analisi della situazione 74.8% del totale delle sperimentazioni Ministero della Salute I primi 30 Comitati Etici sono coordinatori del Roma 2003 Direzione Generale Valutazione Medicinali e Farmacovigilanza Sperimentazione Clinica Team Work Sponsor Sperimentatori Regioni Ministero della Salute Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Ministero della Salute CE Direttiva 2001/20/CE (4/4/2001) Art. 11 - Banca Dati Centrale Europea tutti i paesi membri inviano i dati delle SC svolte nel proprio paese alla BDCE (l’Italia tramite l’OsSC) Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Roma 2003 Ministero della Salute Nuova versione dell’OsSC Direzione Generale Valutazione Medicinali e Farmacovigilanza Ministero della Salute Banca Dati Centrale Europea Ministero della Salute Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Nuovo OsSC Principali novità Profilo ISS (per SC di fase I) Ministero della Salute Profilo ASL (per SC in MMG e PLS) Profilo CRO (supporto alle aziende) Utilities per i CE Registrazione reazioni avverse Reportistica on-line (per Regione, singola struttura, azienda, CE, etc.) Direzione Generale Valutazione Medicinali e Farmacovigilanza Roma 2003 Dalla superiorità alla non-inferiorità: problemi aperti prof. Marubini Dalla superiorità alla non inferiorità: problemi aperti Prof. Ettore Marubini Istituto di Statistica Medica e Biometria Università degli Studi di Milano Min Sal 18/03/03 (1) NEW ENGLAND JOURNAL of MEDICINE 16th october 1997 vol. 337 •A comparison of continuous infusion of alteplase with double-bolus administration for acute myocardial infarction (COBALT investigators) pag. 1124-1131. •A comparison of reteplase with alteplase for acute myocardial infarction (GUSTO III investigators) pag. 1118-1123 Min Sal 18/03/03 (2) Notazioni di base Trattamento di Riferimento (controllo attivo): R Trattamento Sperimentale (nuovo): T Efficacia: vera proporzione di risposte positive, π p: realizzazione empirica di π Min Sal 18/03/03 (3) SCCR di Superiorità Programmata per scoprire la differenza: ∗ T R π −π =δ tra le medie vere dei pazienti trattati con T e quelli trattati con R. Tale differenza è l’attesa giudicata importante clinicamente per adottare un nuovo trattamento Dimensione dello studio e analisi dei risultati in termini di test di ipotesi secondo Neyman-Pearson Min Sal 18/03/03 (4) SCCR di Equivalenza (I) Programmata per confermare l’assenza di una differenza Margine di equivalenza clinica = ε , la più ampia differenza, in valore assoluto, clinicamente accettabile, tra gli effetti dei trattamenti così che una differenza maggiore di questa avrebbe importanza sul piano pratico. Dimensione dello studio e analisi dei risultati in termini di intervallo di confidenza secondo Makuch e Simon (1978) Min Sal 18/93/03 (5) SCCR di Equivalenza (II) di Equivalenza Dimostrazione Mancata dimostrazione -ε 0 ε Sull’asse delle ascisse è riportata la vera differenza tra gli effetti dei due trattamenti a confronto (π R − π T ) Min Sal 18/03/03 (6) SCCR di Non -Inferiorità (I) Programmata per provare che T non è peggio di R. Implica la definizione del margine di tolleranza ε L’interesse del clinico è ora rivolto alla differenza in una sola direzione. Dimensione dello studio e analisi dei risultati in termini di intervallo di confidenza. Le SCCR di Non-Inferiorità sono più frequenti delle SCRR di Equivalenza. In Sl 18/03/03 (7) SCCR di Non -Inferiorità (II) Dimostrazione di Non- Inferiorità Mancata dimostrazione ε 0 Sull’asse delle ascisse è riportata la vera differenza tra gli effetti dei due trattamenti a confronto π − π ( Min Sal 18/03/03 (8) R T ) Ipotesi nulle e Ipotesi alternative SCCR di Superiorità: Ηo :π R − πT ≥ 0 SCCR di Non-Inferiorità Η a :π −π R T < 0 (Blackwelder, 1982) Η 0 :π R − π T ≥ ε Ηa :πR −πT < ε Min Sal 18/03/03 (9) ε 0 Regioni compatibili con le ipotesi Superiorità clinica di T π R −πT < 0 Tolleranza clinica 0 <π R −πT < ε Min Sal 18/03/03 (10) Esatta equiattività π R − π T = 0 Inferiorità clinica di T π R − πT ≥ ε SCCR COBALT (I) “…Thus besides offering the advantage of ease of use, double bolus alteplase (T) might be at least as effective as accelerated infusion (R) as used in the GUSTO I study. The current trial was performed to test this hypothesis.” Min Sal 18/03/03 (11) SCCR COBALT (II) End Points and Statistical Analysis “The primary end point was death from all causes at 30 days. The aim of the trial was to demonstrate therepeutic equivalence. Double bolus alteplase was to be considered at least equivalent to accelerated infusion if the upper boundary of the one sided 95 percent confidence interval of the difference in 30 days mortality did not exceed 0 .40 percent point.” ε = 0 . 004 Min Sal 18/03/03 (12) SCCR COBALT (III) End Points and Statistical Analysis “….0.40 per cent point. This value represented the lower 95 percent confidence limit of the 1 percent absolute difference in 30-day mortality between an accelerated infusion of alteplase and streptokinase that was observed in GUSTO I Trial.” Min Sal 18/03/03 (13) SCCR COBALT (IV) End Points and Statistical Analysis Da GUSTO I nS = 20173 m S = 0 . 073 n A = 10344 m A = 0 . 063 p S = 0.927 p A = 0.937 SCCR di superiorità p A − p S = 0 . 01 I.C. 95 % (0.0041 - - - - - - - -0.0159) Min Sal 18/03/03 (14) SCCR COBALT (V) End Points and Statistical Analysis “We assumed a 30 day mortality rate of 6.3 percent with accelerated infusion of alteplase , …, and a 30-day mortality rate with double bolus alteplase of 5.4 percent. The reduction in the 30 day mortality rate to 5.4 percent …” fu ricavata dallo studio TIMI. π t = (1 − 0.054 ) = 0.946 π R = (1 − 0.063) = 0.937 δ = π R − π t = − 0.009 Min Sal 18/03/03 (15) SCCR COBALT (VI) Dimensione della SCCR (Makuch e Simon, 1978 ) N = 2n = 2 Vincolo: (z 1−α +z ) [π (1 − π ) + π (1 − π )] 2 1− β R R (ε − δ ) T T 2 ε >δ α = 0.05 (test 1 coda) N=2 x 4029=8058 Min Sal 18/03/03 (16) β = 0.20 SCCR COBALT (VII) Curva di potenza π R = 0 .9 3 7 , ε= 0 .0 0 4 , α = 0 .0 5 , β = 0 .2 0 , n = 4 0 2 9 1 .0 0 0 .9 0 0 .8 0 0 .7 0 1 -β 0 .6 0 0 .5 0 0 .4 0 0 .3 0 0 .2 0 0 .1 0 0 .0 0 -0 .0 3 -0 .0 2 -0 .0 1 0 .0 0 0 .0 1 0 .0 2 0 .0 3 πR - πT Min Sal 18/03/03 (17) SCCR COBALT (VIII) Curva di potenza: alcuni punti π R − π -0.009 -0.0045 0.00 0.004 La scelta di T 1 - β 0.80 0.481 0.182 0.05 π R − π T = −0.009 fu clinicamente giustificata o servì solo a permettere il calcolo di N compatibile con una dimensione dello studio economicamente accettabile? Min Sa 18/03/03 (18) SCCR COBALT (IX) Riusultati nR=3384 nT=3585 mR=0.0753 mT=0.0798 pR=0.9247 pT=0.9202 pR-pT=0.0045 (>ε) L.S. I.C. 95%: 0.0149 Non - Inferiorità non dimostrata Min Sal 18/03/03 (19) SCCR COBALT (X) End points and Statistical Analysis Supporto razionale per la scelta del margine ε è fornita da: “ …Thus if equivalence was demonstrated according to the criterion (ε=0.004), superiority over streptokinase could be claimed.” Min Sal. 18/0303 (20) Il documento ICH -10 suggerisce due criteri per la scelta del margine ε: •1. The detemination of the margin in a non-inferiority trial is based on both statistical reasoning and clinical judgement, and should reflect uncertainities in the evidence on which the choice is based, and should be suitably conservative. •2. This non inferiority margin cannot be greater than the smallest effect size that the active drug would be reliably expected to have compared with placebo in the setting of a placebo-controlled trial Min Sal 18/03/03 (21) (a) 1. Historical Effect of Active Control versus Placebo is of a specified size and there is belief that is maintened in the present trial (C>P) Control Placebo (b) 2. Trial has the ability to recognizze the test drug within non-inferiority margin ε of control Placebo 0.8(C.-P.) Test Control 3. and Superior to a Placebo by a specified amount Placebo Min Sal. 18/03/03 (22) Test Control Documento CPMP/EWP/482/99 Switching the objective of a trial from non-inferiority to superiority is feaseble provided: • The trial has been properly designed and carried out in accordance with the strict requirement of a non-inferirority trial. • Actual p-values for the superiority are presented to allow independent assessment of the strenght of the evidence. • Analysis according to the intention-to-treat principle is given greatest emphasis Min Sal 18/03/03 (23) SCCR GUSTO III (I) “…we tested the primary hypothesis that the mortality rate 30 days after acute infarction would be significantly lower with reteplase than with alteplase.” SCCR di superiorità: reteplase vs. alteplase Min Sal. 18/03/03 (24) SCCR GUSTO III (II) Statistical Analysis “The study design required the enrollment of 15,000 patients in order to have at least 85% power to detect a 20% relative reduction in mortality with reteplase as compared to alteplase.” Min Sal. 18/03/03 (25) SCCR GUSTO III (III) Da GUSTO I: π A = 0.063 δ = 0.063x 0.20= 0.0126 π R = 0.0504 α = 0.05 (due code) N=15,000 Min Sal. 18/03/03 (26) nel rapporto 2R:1A β = 0.20 SCCR GUSTO III (IV) Risultati mR = 0.0747 pR=0.9253 mA = 0.0724 pA=0.9276 pA-pR=0.0023 I.C. 95% (-0.00657-----------0.01117) Min Sal. 18/03/03 (27) SCCR GUSTO III (V) Discussion “The chief finding of this trial is that reteplase is not superior to alteplase for the treatment of acute myocardial infarction.” Affermazione assolutamente criticabile perché gli Autori non predefinirono alcun margine ε di non- inferiorità quando pianificarono la SCCR di superiorità. Min Sal. 18/03/03 (28) SCCR GUSTO III (VI) Due scenari alternativi 1.ε = 0.004 da COBALT: la non inferiorità non sarebbe provata 2.ε = 0.01 da GUSTO I (differenza tra alteplase e streptokinasi): la non-inferiorità non sarebbe provata dato che L.S. di I.C. 95% = 0.01117 > ε Min Sal 18/03/03 (29) Documento CPMP/EWP/482/99 Switching the objective of a trial from superiority to non-inferiority may be feaseble provided: •The non- inferiority margin with respect to the control treatment was pre-defined or can be justified. (The latter is likely to prove difficult and to be limited to rare cases where there is a widely accepted value for ε). •Analysis according to the intention-to-treat principle and PP analysis, showing confidence intervals and p-values for the null hypothesis of inferiority, give similar findings. Min Sal. 18/03/03 (30) Documento CPMP/EWP/482/99 (ctd) •The trial was properly designed and carried out in accordance with the strict requirements of a non- inferiority trial (see ICH-E9 and E10) •The sensitivity of the trial is high enough to ensure that it is capable of detecting relevant differences if they exist. •There is direct or indirect evidence that the control treatment is showing its usual level of efficacy. Min Sal. 18/03/03 (31) Methodological Attribute Studies Adhering to Attribute (n=88), n (%) Statement of research aim Aim of equivalence Proportionate difference between entities being compared < 20% Quantitative boundary chosen Method of stochastic testing Not done Failed test for superiority Tested for equivalence Required sample size calcluated 50 (57) 45 (51) 51 (58) 20 (23) 9 (10) 59 (67) 20 (23) 29 (33) W.L. Greene, J. Concato, A.R. Feinstein, Ann.of Inter. Med. 2000; 132:715-722 Min Sal 18/03/03 32 Disegni sequenziali per gruppi prof. Grigoletto Ministero della Salute Direzione Generale della Valutazione dei Medicinali e Farmacovigilanza Sperimentazione Clinica Workshop Le competenze biostatistiche nell’ambito dei Comitati Etici locali Disegni sequenziali per gruppi Francesco Grigoletto Università degli Studi di Padova ________________________ Società Italiana di Statistica Medica ed Epidemiologia Clinica Istituto Superiore di Sanità Roma, 18 marzo 2003 Comitato Etico per la Sperimentazione Clinica Azienda Ospedaliera di Padova Attività 1999-2002 Protocolli Esaminati N=602 Area Oncologica N=84 Fase II N=47 Campione prefissato N=7 Area Non Oncologica N=518 Fase III N=35 Multistadio N=40 Gehan (N=3) Fleming (N=6) Simon (N=27) Chen (N=4) Campione prefissato N=35 Altro N=2 Gruppi sequenziali N=2 Pocock (N=2) Caratteristiche dei Disegni di Fase II (qui considerati) • Obiettivo: Determinare se una nuova procedura di trattamento ha una efficacia sufficiente per procedere ad una valutazione comparativa di Fase III • Bracci: Gruppo singolo • End point: Risposta (completa e/o parziale) al trattamento (variabile dicotomica) • Follow-up: Breve (generalmente inferiore ai 24 mesi) Problema di verifica d’ipotesi • Ipotesi: H0: π ≤ p0 H1: π ≥ p1 essendo: π = p0 = p1 = Proporzione di risposte (successi) in una definita popolazione Tasso massimo di inefficacia Tasso minimo di efficacia • Vincoli per i rischi di errore: Pr(Rifiuto di H0H0) ≤ α Pr(Rifiuto di H1H1) ≤ β Disegni possibili • Numerosità predefinita • Sequenziale (con analisi dopo ogni paziente completato) • Multistadio (sequenziale per gruppi, con analisi dopo completamento di ciascun gruppo) Disegni Multistadio • Vantaggi: – Numerosità campionaria attesa inferiore (a parità di rischi di errore) – Riduzione tendenziale dell’esposizione ad un trattamento inefficace – Tendenziale disponibilità anticipata di un trattamento efficace • Svantaggi: – Maggiore complessità formale – Maggiore impegno di gestione Struttura dei Disegni Multistadio • Numero massimo di stadi: K • Unità incluse ad ogni stadio: n1, n2,.…., nK • Valori soglia di accettazione: A1, A2,….., AK • Valori soglia di rifiuto: R1, R2,….., RK (Ai < Ri) • Decisione allo stadio imo basata sul numero di successi Si: − Si rifiuta H0 se Si ≥ Ri − Si accetta H0 se Si ≤ Ai − Si passa allo stadio successivo altrimenti Disegno di Gehan (1961) • Due stadi (n1, n2) • Al primo stadio: – si accetta H0 se S1/n1 = 0 – altrimenti, si passa al secondo stadio (non si può concludere per l’efficacia) • n1 si ottiene dall’equazione: β1= Pr(S1=0p1) = (1- p1)n1 (n1 =14 per p1=0,20 e β1=5%) • Secondo stadio finalizzato alla stima di π, specificandone la precisione (non occorre prefissare p0 e α) • Tavole di numerosità in Gehan (1961) e Machin et al(1996) Disegno di Fleming (1982) • Numero di stadi K arbitrario (generalmente 2 o 3) • Parametri da specificare: K, p0, p1, α, β • Numerosità totale N calcolata come nello stadio singolo • N è ripartito tra i K stadi arbitrariamente (in genere equamente) • Ciascuno stadio permette di accettare l’ipotesi di inefficacia (π ≤ p0) o l’ipotesi di efficacia (π ≥ p1) • All’ultimo stadio il test fa riferimento ad un unico valore critico definito in funzione di α e β • Numerosità per varie combinazioni dei parametri in Fleming (1982) Disegni di Simon (1989) • Numero di stadi K= 2 • 1 - Disegno ottimo: minimizza il numero medio di pazienti (ASN) quando π=p0 per prefissati rischi di errore α e β • 2 - Disegno minimax: minimizza la numerosità massima richiesta (n=n1+n2) che soddisfa i rischi α e β quando π=p0 • Numero di pazienti a ciascuno stadio determinata dai vincoli di minimizzazione • Interruzione anticipata al primo stadio solo per inefficacia (talora dopo troppo lunghe sequenze di insuccessi) • Numerosità derivate utilizzando la binomiale per alcune combinazioni dei parametri in Simon (1989) e tramite il pacchetto PASS 2000 (J. Hintze, Kaysville, Ut) con metodo iterativo Esempio di disegni ottimale e minimaxa (Simon 1989) Rifiuta il farmaco se il tasso di risposta a Disegno ≤r1/n1 ≤r/n ASN(p0) PET(p0) Ottimale 1/10 5/29 15,0 0,74 Minimax 1/15 5/25 19,5 0,55 Per entrambi si è posto: p0=0,10, p1=0,30, α = 0,05, β =0,20. PET = Probability of Early Termination Output di PASS per un disegno a due stadi con i parametri specificati (1) Two-Stage Clinical Trials Sample Size Page/Date/Time 1 13/03/03 19.12.19 Possible Designs For P0=0.050, P1=0.250, Alpha=0.050, Beta=0.200 N1 R1 PET N R Ave N Alpha Beta Constraints Satisfied 16 2 0.000 16 2 16.00 0.043 0.197 Single Stage 12 0 0.540 16 2 13.84 0.043 0.199 Minimax 9 0.630 17 2 11.96 0.047 0.188 Optimum 0 Output di PASS per un disegno a due stadi con i parametri specificati (2) Two-Stage Clinical Trials Sample Size Possible Designs For P0=0,100, P1=0,250, Alpha=0,050, Beta=0,100 N1 R1 PET N R Ave N Alpha Beta Constraints Satisfied 55 9 0,000 55 9 55,00 0,044 0,089 Single Stage 31 3 0,624 55 9 40,03 0,042 0,099 Minimax 28 3 0,695 57 9 36,86 0,048 0,099 Optimum Disegno di Chen (1997) • Estende a K=3 stadi i disegni di Simon (ottimale e minimax) • Supera il problema di trattare un numero “eccessivo” di pazienti con un farmaco inefficace • Riduce la numerosità campionaria media di circa il 10% (non sempre) • Numerosità: – – – riportate in Chen (1989) per alcuni parametri programma in FORTRAN disponibile dall’autore PASS, versione 2003 Three-Stage Phase II Sample Size Page/Date/Time 1 13/03/03 19.12.19 Possible Designs For P0=0.500, P1=0.700, Alpha=0.050, Beta=0.200 Stage 1 Stage 2 Stage 3 R1/N1 R2/N2 R3/N3 Ave N 23/37 23/37 23/37 37.00 7/16 13/25 23/37 25.31 6/13 13/24 24/39 22.12 Stage 1 Pet P0 0,000 0.402 0.500 Overall Beta Pet P0 Alpha 0.000 0.049 0.673 0.048 0.759 0.048 Constraints Beta Satisfied 0.193 Single Stage 0.199 Minimax 0.199 Optimum Report Definitions N1 is the sample size in the first stage. R1 is the drug rejection number in the first stage. N2 is the sample size in the first and second stages. R2 is the drug rejection number in the second stage. N3 is the combined sample size of all three stages. R3 is the drug rejection number in the third stage. Stage 1 PET P0 is the probability of early termination at the first stage. Stage 2 PET P0 is the probability of early termination at the second stage. AVE N is the average sample size if this design is repeated many times. Alpha is the probability of rejecting that P<=P0 when this is true. Beta is the probability of rejecting that P>=P1 when this is true. P0 is the response proportion of a poor drug. P1 is the response proportion of a good drug. Comitato Etico: Aspetti da verificare in un protocollo oncologico di Fase II • Chiara definizione degli endpoint che indicano successo • Indicazione del disegno utilizzato (con riferimento bibliografico) e sua giustificazione • Specificazione di tutti i parametri necessari a caratterizzare il disegno (in particolare p0 e p1) e loro giustificazione • Numerosità campionaria dei singoli stadi • Inclusione di stime intervallari nelle analisi • Impegno ad informare il CE sui risultati intermedi Sperimentazioni cliniche comparative di Fase III: Analisi intermedie (disegni con gruppi sequenziali) • Scopo: cautelarsi verso inattese e rimarchevoli differenze tra i gruppi di trattamento • Disegno: numerosità prefissate dei gruppi di trattamento, con analisi intermedie per saggiare l’eventuale opportunità di una conclusione anticipata dello studio Giustificazione in termini di: • Eticità: tendenzialmente riduce l’esposizione a un trattamento inferiore o anticipa la disponibilità di un trattamento superiore • Risparmio: di tempo e risorse • Qualità: può evidenziare e rimediare procedure scorrette Trial oncologici di Fase III: Analisi intermedie di gruppi sequenziali • Endpoint: sopravvivenza (vari tipi) • Problema 1: una analisi anticipata di sopravvivenza può non assicurare la sensibilità dei disegni a campione prefissato verso differenze tra trattamenti che si manifestano alla fine del periodo di follow-up • Problema 2: aumentando il numero di verifiche, aumenta la probabilità di evidenziare una significatività statistica, anche se è vera H0 (si devono perciò aggiustare i rischi di errore) Valori critici ed errore di I tipo • Numero di analisi intermedie (looks): K • Tempi di verifica: ti (i=1,…, K) • Funzioni test calcolate sui dati cumulati: zi • Valori critici bi (i=1,…, K) (i=1,…, K) tali che: α =Pr(rifiutare H0H0) = = PrH0(zt1 ≥b1 ∪ zt2≥b2 ∪………. ∪ ztK≥bk) Strategia di definizione dei valori critici: (Pocock 1977) • Tempi equispaziati, ossia ti = i/K (i=1,…, K) • Valori critici bi = c (i=1,…, K) tali che: PrH0(zt1≥c ∪ zt2≥c ∪….. ∪ ztk≥c) = α Strategia di definizione dei valori critici: (Haybittle-Peto 1976) • Tempi equispaziati, ossia ti = i/K (i=1,…, K) • Valori critici bi = c (i=1,…, K-1) tali che: PrH0(zt1≥c ∪ zt2≥c ∪….. ∪ ztk≥z1-α) = α Strategia di definizione dei valori critici: (O’Brien-Fleming 1979) • Tempi equispaziati, ossia ti = i/K (i=1,…, K) • Valori critici bi = c (i=1,…, K) tali che: PrH0(zt1 t1 ≥c ∪ zt2 t2 ≥c ∪….. ∪ ztk tk ≥c) = α Valori normali standardizzati e corrispondenti livelli nominali di significatività per tre test sequenziali (K=5, α=5%, 2 code) Disegno O’Brien-Fleming Haybittle-Peto Stadio Pocock 1 2,413 0,016 4,562 0,00001 3,290 0,001 2 2,413 0,016 3,226 0,001 3,290 0,001 3 2,413 0,016 2,634 0,008 3,290 0,001 4 2,413 0,016 2,281 0,023 3,290 0,001 5 2,413 0,016 2,040 0,041 1,967 0,049 Funzione d’uso (spending function) di α a tempi qualsiasi (Lan e DeMets, 1983) t= frazione di tempo sulla durata complessiva del trial frazione di pazienti sul totale • Funzione di α in t tale che: α(0) = 0 α(1) = 1 • Possibili funzioni: α(t) = 2-2Φ(zα/2/ ) t t] α(t) = α ln [1+(e-1) α(t) = α (O’Brien-Fleming) (Pocock) t3/2 • Si calcolano quindi i valori critici corrispondenti ad α(t) • Metodo flessibile (non occorre pre-specificare i tempi e il numero di analisi) Group Sequential - Survival Numeric Results for Two-Sided Logrank Test (Assuming Exponential Survival) Total Total Sample Required Power Size (N) Events Alpha 0,901100 236 142 0,0500 Proportion Beta Surv. (S1) Surv. (S2) 0,098900 0,3000 0,5000 Details when Spending = O'Brien-Fleming, N = 236, d = 142, S1 = 0,3000, S2 = 0,5000 Look 1 2 3 4 5 Time 0,2000 0,4000 0,6000 0,8000 1,0000 Lower Bndry -4,87688 -3,35695 -2,68026 -2,28979 -2,03100 Upper Bndry 4,87688 3,35695 2,68026 2,28979 2,03100 Nominal Alpha 0,000001 0,000788 0,007357 0,022034 0,042255 Drift 3,28512 Group Sequential - Survival Page/Date/Time 3 14/03/03 17.58.49 O'Brien-Fleming Boundaries with Alpha = 0,05 5 4 3 Z Value 2 Upper 1 0 1 2 3 4 5 -1 Lower -2 -3 -4 -5 Look Power 0,000328 0,100414 0,448228 0,747752 0,901100 Comitato Etico: Aspetti da verificare in un protocollo oncologico di Fase III • Chiara definizione degli endpoint (in particolare le condizioni di sopravvivenza previste) • Indicazione di eventuali analisi intermedie di qualsiasi tipo pianificate (FDA Guidelines) • Se sono previste analisi intermedie equispaziate nel tempo, specificazione di: - numero K - tempi di osservazione - distribuzione di α • Se sono comunque previste analisi intermedie, specificazione della funzione d’uso di α • Inclusione di stime intervallari nelle analisi di sopravvivenza pianificate Aggiustamenti dei livelli di significatività e di confidenza: necessità e opportunità Riferimenti bibliografici CPMP – Points to consider on multiplicity issues in clinical trials ICH Harmonised Tripartite Guideline – Statistical principles for clinical trials dr. Cesana Le competenze biostatistiche nell’ambito dei Comitati etici locali Aggiustamenti dei livelli di significatività e di confidenza: necessità ed opportunità Dr. Bruno Mario CESANA Ospedale Maggiore di Milano, IRCCS Direzione Scientifica - Laboratorio Epidemiologico e-mail: [email protected] Roma 18 Marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC “International Conference on Harmonization (ICH) E9 Guideline: STATISTICAL PRINCIPLES for CLINICAL TRIALS”. Expert Working Group (1,2) da: “Committee for Proprietary Medicinal Products (CPMP) Guideline – Biostatistical Methodology in Clinical Trials in Applications for Marketing Authorisations for Medicinal Products, December 1994" (2,3). •FDA (USA): Guideline for the Format and Content of the Clinical and Statistical Sections of a New Drug Application, July 1988). •Japanese Ministry of Health and Welfare: (Guidelines on the Statistical Analysis of Clinical Studies, March 1992). La ICH E9 adottata dal CPMP (marzo 1998) è divenuta operativa in Europa. E’ poi stata adottata negli USA ed in Giappone. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 2 “The statistical principles outlined in the ICH E9 Guideline are scientifically correct and should be adhere to by both European Member States and companies” (5). “…adherence to the guideline is a must for companies…” (5). “To prevent delay in receiving marketing authorizations, it is strongly recommended that attention be paid to the statistical principles outlined in ICH E9 when designing new clinical development programmes” (5). “…analyses presented allow an assessment of the drug’s risk / benefit to be carried out, part of this being that a good estimate of the size of the potential benefit is available (6). ICH E9 provides statistical advice that if followed can help to ensure that this is the case” (6). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 3 Lo “Statistical Analysis Plan” a cui la ICH E9 fa esplicito riferimento: paragraph V: Data Analysis Considerations section: 5.1 “Prespecification of the Analysis deve essere compilato in accordo ai suggerimenti della ICH E9. Glossary: a statistical analysis plan is a document that contains a more technical and detailed elaboration of the principal features of the analysis described in the protocol, and includes detailed procedures for executing the statistical analysis of the primary and secondary variables and other data. “… the final statistical model based on a formal blind review”. Una specifica sezione della ICH E9 fa riferimento a: ICH E9 – 5.6: Adjustment of Significance and Confidence Levels. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 4 La ICH E9 sostiene l’approccio frequentista di Neyman e Pearson (1928, 1933). “When multiplicity is present, the usual frequentist approach to the analysis of clinical trial data may necessitate an adjustment to the type I error”. Glossary: frequentist methods: statistical methods, such as significance tests and confidence intervals, which can be interpreted in terms of the frequency of certain outcomes occurring in hypothetical repeated realisations of the same experimental situation. Per Neyman e Pearson (1928, 1933) nel contesto di una formulazione che fa riferimento ad una ipotetica infinita popolazione di esperimenti corrispondente a ripetizioni dell’esperimento effettivamente effettuato, si delineano le nozioni di probabilità di errore di I tipo (la soglia di significatività α) e di II tipo (β) come rispettivamente le probabilità di rifiutare (non accettare) vere H0 e di non rifiutare (accettare) false H0, facendo riferimento alla distribuzione generata dalla suddetta ipotetica infinita popolazione di esperimenti data Ha. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 5 TEORIA DEL TEST DI SIGNIFICATIVITÀ: Ipotesi nulla: H0 ed ipotesi alternativa: Ha. La pertinente distribuzione di probabilità della statistica test, dati gli assunti distribuzionali (esatti o asintotici), Calcolo della probabilità, data H0, di ottenere un valore pari o superiore (inferiore) a quello calcolato (livello di significatività, p), Soglia del livello di significatività (α): per p ≤ α si può essere fiduciosi di aver ottenuto una sufficiente evidenza a rifiutare (non accettare) H0 per sostenere Ha; dati i valori sperimentali, H0 diviene talmente poco probabilisticamente plausibile da essere considerata “non plausibile o non ulteriormente sostenibile”. La potenza (1-β) di un esperimento ad evidenziare un prefissato effetto è il valore di probabilità a cui H0 dovrebbe essere rifiutata. Per – Comparison Error Rate (PCE): la proporzione attesa di errori di I tipo. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 6 ICH E9: section: 5.5 estimation, confidence intervals and hypothesis testing. It is important 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. The approach of setting type I errors for one-sided tests at half the conventional type I error used in two-sided tests is preferable in regulatory settings. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 7 DEFINIZIONI: livello di confidenza Il calcolo di una stima intervallare del parametro di interesse: (θ: differenza tra il nuovo trattamento e lo standard e/o il placebo). Si richiede che la probabilità che il parametro di interesse (θ) sia compreso tra il limite inferiore (L0) ed il limite superiore (L1) sia pari a 1-α, essendo 1-α il coefficiente di confidenza: Pr (L0 ≤ θ ≤L1) = 1 - α Da questa formulazione che porta ad affermare che il parametro di interesse è compreso nell’intervallo con probabilità 1-α, in accordo all’approccio frequentista di Neyman e Pearson, in cui il parametro è una costante e gli intervalli sono essi stessi variabili casuali (analogamente al limite superiore ed inferiore), si conclude che l’affermazione che il parametro è compreso nei limiti calcolati ha la probabilità di essere corretta pari a 1-α e quindi nel 100(1-α)% dei casi nell’ambito di una serie ripetuta di esperimenti (in the long run). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 8 ICH E9 Section 5.6: Multiplicity may arise, for example, from: -multiple primary variables (see section 2.2.2), -multiple comparisons of treatments, -repeated evaluation over time and/or interim analyses (see section 4.5). Methods to avoid or reduce multiplicity are sometimes preferable when available, such as: -the identification of the key primary variable (multiple variables), -the choice of a critical treatment contrast (multiple comparisons), -the use of a summary measure such as ‘area under the curve’ (repeated measures). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 9 In confirmatory analyses, any aspects of multiplicity which remain after steps of this kind have been taken should be identified in the protocol; adjustment should always be considered and the details of any adjustment procedure or an explanation of why adjustment is not thought to be necessary should be set out in the analysis plan. Paragrafo 1.2 scope and direction: •The focus of this guidance is on statistical principles. •It does not address the use of specific statistical procedures or methods. •Specific procedural steps to ensure that principles are implemented properly are the responsibility of the sponsor. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 10 … the actual responsibility for all the statistical work associated with clinical trials will lie with an appropriately qualified and experienced statistician, as indicated in ICH E6…(guideline for good clinical practice, 1996). For each clinical trial contributing to a marketing application, all important details of its design and conduct and the principal features of its proposed statistical analysis should be clearly specified in a protocol written before the trial begins. The extent to which the procedures in the protocol are followed and the primary analysis is planned a priori will contribute to the degree of confidence in the final results and conclusions of the trial. The principles outlined in this guidance are primary relevant to clinical trials conducted in the later phases of development, many of which are confirmatory trials of efficacy. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 11 Section 2.2.2 primary and secondary variables Primary variable (‘target’ variable, primary endpoint) should be the variable capable of providing the most clinically relevant and convincing evidence directly related to the primary objective of the trial. There should generally only one primary variable. (the primary variable should generally be the one used when estimating the sample size). To avoid multiplicity concerns arising from post hoc definitions, it is critical to specify in the protocol the precise definition of the primary variable as it will be used in the statistical analysis. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 12 Section: 2.2.3 composite variables Multiple measurements associated with the primary objective …. to integrate or combine ….into a single or ‘composite’ variable, using a pre-defined algorithm. This approach addresses the multiplicity problem without requiring adjustment to the type I error. Mortalità, recidiva di infarto miocardico, congestizia, disfunzione del ventricolo sn. Overall mortality, graft + patient survival. (analisi per singolo end-point). insufficienza cardiaca Considerazioni (Cannon, 1997, (7), Gent, 1997, (8) ): -statistiche: bassa incidenza – potenza dello studio, -patofisiologiche: stessa malattia di base, -clinico – terapeutiche: effetto “globale” della terapia. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 13 Section: 2.2.4 global assessment variables Glossary: a single variable, usually a scale of ordered categorical ratings, which integrates objective variables and the investigator’s overall impression about the state or change in state of a subject. CGI: Clinical Global Improvement. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 14 Section: 2.2.5 multiple primary variables It may sometimes be desirable to use more than one primary variable, each of which (or a subset of which) could be sufficient to cover the range of effects of the therapies. The effect on the type I error should be explained because of the potential for multiplicity problems (see section 5.6); the method of controlling type I error should be given in the protocol. The extent of intercorrelation among the proposed primary variables may be considered in evaluating the impact on type I error. If the purpose of the trial is to demonstrate effects on all of the designated primary variables, then there is no need for adjustment of the type I error, but the impact on type II error and sample size should be carefully considered. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 15 Section: 4.5 interim analysis and early stopping Glossary: interim analysis: any analysis intended to compare treatment arms with respect to efficacy or safety at any time prior to the formal completion of a trial. When an interim analysis is planned with the intention of deciding whether or not terminate a trial, this is usually accomplished by the use of a group sequential design which employs statistical monitoring schemes as guidelines (see section 3.4: group sequential designs). The protocol should describe the schedule of interim analyses, or at least the considerations which will govern its generation, for example if flexible alpha spending function approaches are to be employed. The stopping guidelines and their properties should be clearly described in the protocol or amendments. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 16 One-day Discussion Forum (London, October 1998) arranged by Statisticians in the Pharmaceutical Industry (PSI), a United Kingdom-based Professional Association of Statisticians Interested in Pharmaceutical Industry (9). Workshop 4: multiplicity. the application of Statistics in the primary / secondary endpoints and Q3: what are the preferred methods of adjustment for multiple endpoints ?. -Bonferroni and hierarchical procedures. Q1: what are the preferred strategies for handling multiple treatment comparisons ?. -use of closed test procedures, -testing the overall treatment effect before considering any individual comparisons, -use of Dunnett’ s (10) procedure, and -use of Bonferroni correction. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 17 Points to Consider on Multiplicity Issues in Clinical Trials (CPMP/EWP/908/99). (Adoption by CPMP – September 2002) Multiplicity of inferences is present in virtually all clinical trials. α = 0.025; five subgroups: 1 - (1- α)5 = 1 - 0.88 = 0.12 o 12%. “If statistical tests are performed on five subgroups, independently of each other and each at a significance level of 2.5% (one sided directional hypotheses), the chance of finding at least one false positive statistically significant test increases to 12%.” Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 18 “Control of the study-wise rate of false positive conclusions at an acceptable level α is an important principle…”. “Throughout this document the term “control of type I error“ rate will be used as an abbreviation for the control of the family-wise type I error in the strong sense, i.e., there is control on the probability to reject at least one true null hypothesis, regardless which subset of null hypotheses happens to be true.” Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 19 2)-Adjustment of multiplicity – when is it necessary and when is it not ?. 3)-How to interpret significance with respect to multiple secondary variables and when can a claim be based on one of these ?. 4)-Reliable conclusions be drawn from a subgroup analysis, and restriction of the licence to a subgroup. 5)-How should one interpret the analysis of “responders” in conjunction with the raw variables ?. 6)-How should composite endpoints be handled statistically with respect to regulatory claims ?. A separate document may cover interim analyses or stepwise designed studies. “Potential multiplicity issues concerning the analysis of repeated measurements are not considered in this document (summary measures, pre-specified endpoint).” [trend analysis]. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 20 2)- Adjustment of multiplicity – when is it necessary and when is it not ?. “No adjustment of the type I error: a study with two treatment groups, with a single primary variable and with a confirmatory statistical strategy that prespecifies just one single null hypothesis relating to the primary variable and no interim analysis”. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 21 “For the purpose of estimation and for the appraisal of the precision of estimates, confidence intervals are of paramount importance but methods for their construction that are consistent with the tests are not available for many of the more complex multiple-level-α-tests (or more generally closed tests) aiming at controlling the type I error”. “Because alternative methods to deal correctly with multiplicity are often available which may lead to different conclusions, predefinition of the preferred multiple-level-α-test is necessary”. “To avoid problems in interpretation, details of the procedure should be contained in the study protocol or the statistical analysis plan”. “If a multiple test situation occurs which has not foreseen, a conservative approach will be necessary e.g. Bonferroni’s or a related procedure. Inherently there will be a loss of power.” Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 22 2.1-Multiple primary variables – when no formal adjustment is needed: 2.1.1-Two or more primary variables are needed to describe clinically relevant treatment benefits. “Statistical significance is needed for all primary variables. therefore, no formal adjustment is necessary”. 2.1.2-Two or more primary variables ranked according to clinical relevance “No formal adjustment is necessary. However, no confirmatory claims can be based on variables that have a rank lower than or equal to that variable whose null hypothesis was the first that could not be rejected”. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 23 2.2-Analysis sets “In general, multiple analyses on varying subsets of subjects or with varying measurements for the purpose of investigating the sensitivity of the conclusions drawn from the primary analysis should not be subjected to adjustment for type I error”. 2.3 - Alternative statistical methods – multiplicity concerns 2.4 - Multiplicity in safety variables Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 24 2.5 - Multiplicity concerns in studies with more than two treatment arms. “The discussion is limited to the more common and simple designs. As a general rule it can be stated that control of the family-wise type I error in the strong sense (i.e. application of closed test procedures) is a minimal prerequisite for confirmatory claims”. “It should be remembered that the usual confidence intervals for the pairwise differences between treatment groups are – except for a few instances – not consistent with the closed testing procedures, and are usually too narrow.” Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 25 2.5.1 - The three arm “gold standard” design -the reference drug, -placebo and -the investigational drug. Usually the aims of such a study are manifold: (1)–to demonstrate superiority of the investigational drug over placebo (proof of efficacy); (2)–to demonstrate superiority of the reference drug over placebo (proof of assay sensitivity, see ICH E10 section 2.5.1.1.1); (3)–to demonstrate that the investigational drug retains most of the efficacy of the reference drug as compared to placebo (proof of non-inferiority). “If all of these are objectives, all three comparisons must show statistical significance at the required level, and no formal adjustment is necessary”. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 26 AGGIUSTARE O NO ? •CONTRASTI TRA DUE TRATTAMENTI ATTIVI VERSO IL PLACEBO •CONTRASTI TRA PIÙ TRATTAMENTI. Perché se si confronta A vs. B in un trial e A vs. C in un altro trial è assolutamente non discutibile che la soglia di significatività sia pari ad α in entrambi in casi e se invece si confronta A vs. B e A vs. C in un solo trial si dovrebbe aggiustare ?. Trial con tre trattamenti per una stima più precisa della variabilità e per arruolare un minor numero di pazienti. (Proschan - Waclawiw, 2000). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 27 2.5.2 - Proof of efficacy for a fixed combination “CPMP/EWP/240/95 requires that “each substance of a fixed combination must have documented contribution within the combination”. For a combination with two (mono) components, a 3-arm study. “No formal adjustment of the overall significance level is necessary, because both pairwise comparisons must show statistically significant superiority”.. Multiple-dose factorial designs are employed for the assessment of combination drugs for the purpose: (1)-to provide confirmatory evidence that the combination is more effective than either component alone (CPMP/ICH/387/95 – ICH E4) . This is usually achieved using global test strategies. (2)-to identify an effective and safe dose combination (or a range of useful dose combinations). Appropriate closed test procedures. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 28 2.5.3 - Dose-response studies (NO STAtistical Significance Of Trend dose). “The control of the family-wise type I error in the strong sense is mandatory.” “Specific recommendations are beyond the scope of this document”. “There are various methods published in the relevant literature on closed test procedures with relevance to multiple dose studies that can be adapted to the specific aims and that provide the necessary control on the type I error.” (Bauer: 1997, 1998, Rom: 1994). “...Sometimes a study ... is successful at demonstrating an overall positive correlation of the clinical effect with increasing dose….” “Estimates and confidence intervals from pairwise comparisons of single doses are then used in an exploratory manner for the planning of future studies.” In this case, an adjustment of the type I error is not necessary. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 29 3)-How to interpret significance with respect to multiple secondary variables and when can a claim be based on one of these ?. Un “endpoint secondario” permette di ottenere ulteriori caratterizzazioni cliniche dell’effetto del trattamento ma non è sufficiente a caratterizzarne completamente il beneficio o a supportare una richiesta di registrazione del trattamento (O’Neill, 1997). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 30 3.1 Variables expressing supportive evidence: No claims are intended; confidence intervals and statistical tests are of exploratory nature. 3.2 Secondary variables which may become the basis for additional claims (after the primary objective of the clinical trial has been achieved…. A valid procedure, to deal with this kind of secondary variable is to proceed hierarchically). 3.3 Variables indicative of clinical benefit If not defined as primary variables, clinically very important variables (e.g. mortality) need further study when significant benefits are observed, but the primary objective has not been achieved (O’NEILL, 1997). Moyé (2000): Prospective Alpha Allocation Scheme (PAAS: αE (0.10), αP, αS) SURROGATE ENDPOINTS ? Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 31 4. Reliable conclusions from a subgroup analysis, and restriction of the licence to a subgroup. Reliable conclusions from subgroup analyses generally require pre-specification and appropriate statistical analysis strategies. A licence may be restricted if unexplained strong heterogeneity is found in important sub-populations, or if heterogeneity of the treatment effect can reasonably be assumed but cannot be sufficiently evaluated for important sub-populations. The evaluation of uniformity of treatment effects across subgroups is a general regulatory concern. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 32 Multiple Comparisons Procedures (MCP) Uno dei più importanti e controversi aspetti delle MCP: la scelta della famiglia di inferenze (“family”). •costituiscono una naturale e coerente unità: “contextual relatedness”. •sono considerate contemporaneamente nel processo decisionale (è importante considerare il rischio d’errore). •principio di parsimonia: minor numero possibile. {D vs. P}, {C1 vs. P, C2 vs. P}, {D vs. C1, D vs. C2} Cook & Dunnett (1998): {D vs. P, C vs. P}, {D vs. C} D’Agostino (1993) Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 33 Familywise error rate (FWE) è definita come la probabilità di fare una o più false positive conclusioni per tutte le ipotesi test in una particolare famiglia. FWE = P(rifiutare almeno una delle H01, H02,…,H0k | H01, H02,…,H0k sono tutte vere). Controllare FWE è appropriato se non si può accettare alcun errore di I tipo nella famiglia, indipendentemente da quante delle k ipotesi nulle sono vere. Le procedure di confronti multipli (MCP) controllano la FWE ad α: Pr(almeno una vera ipotesi nulla è falsamente rifiutata) ≤ α. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 34 “controllo debole” della FWE ad α è ottenuto se questa probabilità di errore di I tipo è garantita essere al massimo α quando tutte le ipotesi nulle sono vere. Ad esempio la “protected Least Significance Difference (LSD)” procedura di Fisher (1935). Procedura a due stadi: 1)-la globale H0 è saggiata mediante un test F al livello α, 2)-in caso di rifiuto, tutte le differenze a coppie sono saggiate mediante un test t di Student al livello α. Si effettuano test t multipli ciascuno a livello α solo se un preliminare test F è statisticamente significativo a livello α. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 35 “controllo forte” della FWE ad α è ottenuto se la probabilità di effettuare almeno un errore di I tipo su tutte le ipotesi test della famiglia è al massimo α, indipendentemente da quante ipotesi nulle della famiglia possano essere vere. La seconda procedura di Fisher (1935): “procedura di Bonferroni” ad un singolo stadio. Si effettuano test t multipli (confronti a coppie di k medie, ad esempio) ciascuno al livello α* = α / k , senza un 2 preliminare test F. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 36 CLOSURE PRINCIPLE / METHOD (PERITZ, 1970). CLOSED TESTING METHODS / PROCEDURES “controllo forte” della FWE ad α (errore di I e III Tipo). “closed under intersection” = se H01, H02 ∈ I, allora H01 ∩ H02 ∈ I. Siano date quattro (k) medie (k(k-1)/2 confronti a coppie). Si ottiene la “chiusura” della famiglia costituendo i seguenti set non vuoti di ipotesi: 1)-H1234: µ1 = µ2 = µ3 = µ4 2)-H123: µ1=µ2= µ3; H124: µ1= µ2= µ4; H134: µ1=µ3=µ4; H234: µ2 = µ3 = µ4 3)-H(12)∩(34): µ1=µ2∩µ3=µ4; H(13)∩(24): µ1=µ3∩µ2=µ4;H(14)∩(23): µ1=µ4∩µ2=µ4; 4)-H12: µ1=µ2; H13: µ1=µ3; H14: µ1=µ4; H23: µ2=µ3; H24: µ2=µ4; H34: µ3=µ4; Ognuna di queste ipotesi è saggiata a α [ (3)- a 1-(1-α)1/2, Peritz, 1970]. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 37 Un’ipotesi elementare (minimale), diciamo H12: µ1=µ2, è dichiarata statisticamente significativa, se risultano statisticamente significativi anche i test di significatività che saggiano le ipotesi: H1234, H123, H124, e H(12)∩(34) che comprendono H12. Test di significatività applicati gerarchicamente solo a (set di) ipotesi compresi in set di ipotesi di ordine superiore che sono state rifiutate: si saggia H123, H124, e H234 solo se H1234 è stata rifiutata. Proprietà della “COERENZA”: H(12)∩(34): µ1=µ2∩µ3=µ4 (o H1234) implica anche H12: µ1=µ2 e H34: µ3=µ4; Se H(12)∩(34) (o H1234) non è rifiutata anche H12 e H34 non lo sono. Proprietà della “CONSONANZA”: Se H(12)∩(34): µ1=µ2∩µ3=µ4 è rifiutata, allora almeno una delle due ipotesi che la compongono (H12: µ1=µ2 e H34: µ3=µ4) è rifiutata. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 38 UNA “SCORCIATOIA” (SHORTCUT) DELLA “CLOSED TESTING PROCEDURE” “FREE COMBINATIONS CONDITION” (HOLM, 1979). Ogni partizione di “ m “ ipotesi in due sotto-insiemi (uno in cui le ipotesi sono tutte vere e l’altro in cui le ipotesi sono tutte false) è possibile per almeno qualche punto dello spazio dei parametri. Impiego dei cosiddetti “Intersection-Union (UI) tests” che hanno la proprietà che una qualsiasi “intersezione di una famiglia di ipotesi” (Roy, 1953: H0=∩ i∈ I H0i, I indice di un arbitrario set) è rifiutata se e solo se almeno una delle ipotesi H0i è rifiutata. La regione di rifiuto per H0 è data dalla unione delle regioni di rifiuto per le H0i, i ∈ I. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 39 Se la regione critica (di rifiuto) di ciascuna H0i per i ∈ I è della forma (T0i > ξ ), la statistica per ogni non minimale (intersezione) H0 sarà T0 = max i ∈ I T0i e la sua regione critica sarà T0 > ξ . I valori di T0 così ottenuti sono definiti “UI statistiche”. Si dimostra che una “single-step procedure” è coerente e consonante se e solo se è una UI procedura (Gabriel, 1969). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 40 Quindi per rifiutare una qualsiasi ipotesi elementare, diciamo H01, non è necessario saggiare tutte le “intersezioni ipotesi” che la contengono. E’ sufficiente saggiare direttamente H01 purché la procedura di “testing” sia effettuata in una modalità “stepdown” ordinando le H0i [i valori di probabilità corrispondenti: p(m) ≤ p(m-1) ≤ … ≤ p(1) ] in modo da assicurare la condizione della coerenza. Si saggia l’ipotesi corrispondente al minimo valore p(m) al livello α / m, se questa è rifiutata si saggia l’ipotesi corrispondente al valore di p(m-1) al livello α / (m - 1) e così via; altrimenti la procedura si ferma non rifiutando tutte le ipotesi rimanenti. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 41 Questa è la “Sequentially Rejective Multiple Test Procedure” di Holm (1979), che si basa sulla proprietà della “monotonicità dei valori critici” del test di Bonferroni (p(m) ≤ α/m → p(m) ≤ α/(m –1) → p(m) ≤ α/(m-2)…]. Se dopo aver rifiutato “ j ” ipotesi corrispondenti ai “ j ” più piccoli valori di p [p(m) ≤ p(m-1) ≤ … ≤ p(m-j+1)] invece di saggiare la (j+i)-esima ipotesi al livello α / (m - j) la si saggia al livello α / j* (essendo j* il massimo numero possibile di vere ipotesi nulle dato che “ j ” ipotesi nulle sono già state rifiutate), si applica la procedura modificata proposta da Shaffer (1986). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 42 PROCEDURE SIMULTANEE SIMULTANEOUS TESTING PROCEDURES (STP): Una collezione di test in cui un’ipotesi è rifiutata se T0i > ξ (i ∈ I) dove ξ è una costante critica comune per tutti i test (Gabriel, 1969). (Bonferroni: α* = α / I ; Šidák: α* = 1-(1-α)1 / I) Tukey: (tutti i confronti a coppie (pairwise): MCA “studentized range”) Dunnett: (tutti i confronti con un controllo: MCC) Scheffé (simultaneous confidence intervals) Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 43 PROCEDURE “STEP-WISE”: Step-down: dal “più significativo” valore del test (minimo valore di p) al “meno significativo” (massimo valore di p). Marcus - Peritz - Gabriel (1976), Bonferroni-Holm (1979), Šidák-Holm, Simes (1986), Hommel (1988) Tukey-Welsch (Ryan, Einot, Gabriel, Welsch) Dunnett - Tamhane (1991) Step-up: dal “meno significativo” valore del test (massimo valore di p) al “più significativo” (minimo valore di p). Hochberg (1988), Rom (1990), Benjamini – Hochberg (1995), Dunnett - Tamhane (1992) Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 44 CLASSIFICAZIONE delle MCP IN BASE AI PARAMETRI SU CUI FARE UNA DIRETTA INFERENZA (HSU, 1996) ACC: All-Contrasts Comparisons: k ∑c µ i i i =1 MCA: All-Pairwise Comparisons: µi - µj , per i < j MCB: Multiple Comparisons with the Best: µi - maxj ≠i µj , per i =1,…,k MCC: Multiple Comparisons with the Control: µi - µk , per i = 1,…, k - 1 Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 45 INTERVALLI DI CONFIDENZA: STP (1) γi = I’i θ con I’i = (1, -1, 0,..,0m)’; γi = funzione stimabile dei parametri θ. m m H0i: γi = γ0i verso H1: γi = γ1i (1 ≤ i ≤ m): H0 = I i=1H0i verso H1 = U i=1H1i PrH0 (ti > ξi per qualche i = 1, 2,…,m) = α; ξi = ξ; UI test rifiuta H0 se max(1 ≤ i ≤ m)ti > ξ; PrH0 (max(1 ≤ i ≤ m)ti > ξ) = α. Sotto H0, t1, t2,…, tm sono distribuiti secondo una multivariata (mvariata) distribuzione t (Dunnett e Sobel, 1954, Cornish, 1954) con ν gradi di libertà ed associata matrice di correlazione R={ρij } (1≤i ≠ j≤m). La regione di confidenza per γ a livello (1-α) è data da: γ : γi ∈ [ ± Tα,m,ν, ( ρij ) s (C)1/2 ] per (1 ≤ i ≤ m) γ̂ i Tα,m,ν, ( ρij )è il percentile della multivariata t distribuzione, s è la radice quadrata della varianza d’errore stimata e C è una costante che dipende dal contrasto (funzione stimabile) considerato. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 46 INTERVALLI DI CONFIDENZA: STP (2) Tα,m,ν, ( ρij ) sostituito da: tα*/2,ν con: α* = α / m (Bonferroni), α* = 1 - (1-α)1 / m (Dunn-Šidák). Se ρij = 0: “Studentized Maximum Modulus Distribution” (Tukey, 1953; Roy e Bose, 1953) con parametri m ed i gradi di libertà ν: Mα,m,ν. Per m = k(k-1) / 2 confronti a coppie: “Studentized Range Distribution” (T-procedure di Tukey, 1953) con parametri k ed i gradi di libertà ν : Qα,k,ν. (θi - θj) ∈ [ Yi − Yj ± Qα,k,ν, s (2 / n)1/2 ] per (1 ≤ i ≠ j ≤ m). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 47 INTERVALLI DI CONFIDENZA (3): Stepdown Method: Multiple Comparisons with a Control: No stepwise procedures has a corresponding confidence set (Lehmann, 1986). Bofinger (1987), Stefansson et al. (1988), Dunnett e Tamhane (1991): µ[i] - µk > µˆ [i] − µˆ k − dk −1σˆ 2n con d1 (=tα , υ) < d2 < ...<dk-1 quantili della multivariata (2,…, k-2, k-1) t distribuzione. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 48 MCP - Intervalli di confidenza – Variabili Binomiali (non normali). Impiego della trasformata arcoseno arcsin√p ∼ N(arcsin√π, 1/(4n) ) “bootstrap” e “permutation resampling” (SAS® Proc MULTTEST: single-step / step-down tests) Fisher’s exact test, Cochran-Armitage linear trend test, Freeman – Tukey, Peto mortality – prevalence (log-rank). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 49 Le Guidelines non contemplano la possibilità di confrontare due trattamenti mediante un “test globale” che considera congiuntamente “multiple endpoints”. Metodologia proposta da O’Brien (1984, mediante approccio non parametrico sui dati trasformati in ranghi e parametrico sui dati previamente deviati e standardizzati) ed estesa da Pocock et al. (1987 a qualsiasi statistica test con distribuzione asintotica normale). L’approccio mirava a superare i limiti di un confronto tra due campioni multivariati (test T2 di Hotelling) la cui ipotesi nulla può essere rifiutata senza distinguere tra variabili che cambiano a favore o a sfavore di uno o dell’altro trattamento ed il fatto che la correzione di Bonferroni è conservativa. “Theoretically attractive but it is probably of practical use in only a small minority of trials (Pocock, 1997)”. Le Guidelines non contemplano l’uso di test globali (analisi della varianza, test del χ2) per il confronto di più di due trattamenti. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 50 POTENZA – DIMENSIONE DEL CAMPIONE PER MCP ICH E9: “If the purpose of the trial is to demonstrate effects on all of the designated primary variables, then there is no need for adjustment of the type I error, but the impact on type II error and sample size should be carefully considered”. 10 indipendenti test, tutti con una potenza individuale dello 0.80, la COMPLETE POWER = (0.80)10 = 0.10737. COMPLETE POWER = Pr (rifiutare tutte le H0i che sono false). MINIMAL POWER = Pr (rifiutare almeno una H0i falsa). INDIVIDUAL POWER = Pr (rifiutare una particolare H0i che è falsa). PROPORTIONAL POWER = valore atteso della proporzione di false H0i che sono rifiutate. Simulando 10,000 studi, si calcola la proporzione di false H0i che sono rifiutate per ciascun studio e poi si calcola la media di queste proporzioni per i 10,000 studi. Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 51 POTENZA – DIMENSIONE DEL CAMPIONE PER MCP Usando l’approccio dei confronti multipli basato sugli intervalli di confidenza simultanei, la power è definita come la probabilità che gli intervalli di confidenza comprendano i valori dei veri parametri e siano sufficientemente “piccoli”. MULTIPLE COMPARISONS with a CONTROL (MCC): si deve specificare: 1)- il numero di gruppi (k: il k-esimo è il controllo), 2)- il valore minimo della differenza ω = µi - µk che si vuole dimostrare, 3)- la dimensione iniziale campionaria n (n1, n2,…,nk se non bilanciato), 4)- la potenza (1 - β) richiesta (“Complete Power”), 5)- il livello di significatività (α), 6)- la deviazione standard entro i gruppi (σ). MULTIPLE COMPARISONS with the BEST (MCB). ALL-PAIRWISE COMPARISONS (MCA). Roma, 18 marzo 2003 Osservatorio Nazionale Sperimentazione Clinica ISS / SISMEC 52 Riferimenti bibliografici 1. 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Multiple Tests with Discrete Distributions The American Statistician, 51: 3 - 8, 1997. LIBRI Hochberg Y., Tamhane AC. Multiple Comparison Procedures John Wiley & Sons, 1987 Hsu JC. Multiple Comparisons. Theory and methods Chapman & Hall, London, 1996 Lehman EL. Testing Statistical Hypothesis. John Wiley & Sons, 2nd Ed., 1986 Miller GR. Simultaneous Statistical Inference. McGraw-Hill, 1966; 2nd ed. Springer-Verlag, 1981 Westfall PH., Tobias RD., Rom D., Wolfinger RD., Hochberg Y. Multiple Comparisons and Multiple Tests Using the SAS System Cary, NC: SAS Institute Inc., 1999 EMEA The European Agency for the Evaluation of Medicinal Products Evaluation of Medicines for Human Use London, 19 September 2002 CPMP/EWP/908/99 COMMITTEE FOR PROPRIETARY MEDICINAL PRODUCTS (CPMP) POINTS TO CONSIDER ON MULTIPLICITY ISSUES IN CLINICAL TRIALS DISCUSSION IN THE EFFICACY WORKING PARTY January 2000 TRANSMISSION TO CPMP JuIy 2001 RELEASE FOR CONSULTATION JuIy 2001 DEADLINE FOR COMMENTS DISCUSSION IN THE EFFICACY WORKING PARTY October 2001 June 2002 TRANSMISSION TO CPMP September 2002 ADOPTION BY CPMP September 2002 7 Westferry Circus, Canary Wharf, London, E14 4HB, UK Tel. (44-20) 74 18 84 00 Fax (44-20) 74 18 8613 E-mail: [email protected] http://www.emea.eu.int ©EMEA 2002 Reproduction and/or distribution of this document is authorised for non commercial purposes only provided the EMEA is acknowledged POINTS TO CONSIDER ON MULTIPLICITY ISSUES IN CLINICAL TRIALS 1. INTRODUCTION Multip1icity of inferences is present in virtually all clinical trials. The usual concern with multiplicity is that, if it is not properly handled, unsubstantiated claims for the effectiveness of a drug may be made as a consequence of an inflated rate of false positive conclusions. For example, if statistical tests are performed on five subgroups, independently of each other and each at a significance level of 2.5% (one-sided directional hypotheses), the chance of finding at least one false positive statistically significant test increases to 12%. This example shows that multiplicity can have a substantial influence on the rate of false positive conclusions which may affect approval and labelling of an investigational drug whenever there is an opportunity to choose the most favourable result from two or more analyses. If, however, there is no such choice, then there can be no influence. Examples of both situations will be discussed later. Control of the study-wise rate of false positive conclusions at an acceptable level a is an important principle and is often of great value in the assessment of the results of confirmatory clinical trials. A number of methods are available for controlling the rate of false positive conclusions, the method of choice depending on the circumstances. Throughout this document the term ‘control of type I error’ rate will be used as an abbreviation for the control of the family-wise type I error in the strong sense, i.e., there is control on the probability to reject at least one true null hypothesis, regardless which subset of null hypotheses happens to be true. The issue of setting an appropriate type I error level on a submission level when this includes the need for more than one confirmatory trial is discussed in a separate Points-to-Consider document (CPMP/2330/99 Points to Consider on Application with 1.) Meta-analyses and 2.) One Pivotal study). This document does not attempt to address all aspects of multiplicity but mainly considers issues that have been found to be of importance in recent European applications. These are: • Adjustment of multiplicity — when is it necessary and when is it not? • How to interpret significance with respect to multiple secondary variables and when can a claim be based on one of these? • When can reliable conclusions be drawn from a subgroup analysis? • When is it appropriate for CPMP to restrict licence to a subgroup? • How should one interpret the analysis of “responders” in conjunction with the raw variables? • How should composite endpoints be handled statistically with respect to regulatory claims? There are further areas concerning multiplicity in clinical trials which, according the above list of issues, are not the focus of this document. For example, there is a rapid advance in methodological richness and complexity regarding interim analyses (with the possibility to stop early either for futility or with the claim of effectiveness) or stepwise designed studies (with the possibility for adaptive changes for the future steps). However, due to the importance of the problem and the amount of information specific to this issue it appears appropriate that a separate document may cover these aspects. CPMP/EWP/908/99 1/10 ©EMEA 2002 Interpretations of repeated evaluations of the primary efficacy variable at repeated visits usually do not cause multiplicity problems, because in the majority of situations either an appropriate summary measure has been pre-specified or according to the requirements on the duration of treatment endpoint, primary evaluations are made at pre-specified visits. Therefore potential multiplicity issues concerning the analysis of repeated measurements are not considered in this document. 2. ADJUSTMENT FOR MULTIPLICITY - WHEN IS IT NECESSARY AND WHEN IS IT NOT? A clinical study that requires no adjustment of the type I error is one that consists of two treatment groups, that uses a single primary variable, and has a confirmatory statistical strategy that pre-specifies just one single null hypothesis relating to the primary variable and no interim analysis. Although all other situations require attention to the potential effects of multiplicity, there are many situations where no multiplicity concern arises, for example, having predefined the primary variables and all secondary variables are declared supportive. In the literature, methods to control the overall type I error α are sometimes called multiple-level-α-tests”. Controlling type I error family-wise often (but not always) means that the accepted and pre-specified amount α of type I error has to be split, and that the various null hypotheses have to be tested at the resulting fraction of α. This is usually referred to as ‘adjusting the type I error level’. The algorithms that define how to “spend” α in this way are of different complexity. Often, for the more complex procedures, clinical interpretation of the findings can become difficult. For example, for the purpose of estimation and for the appraisal of the precision of estimates, confidence intervals are of paramount importance but methods for their construction that are consistent with the tests are not available for many of the more complex multiple-level-α-tests (or more generally closed tests) aiming at controlling the type I error. When choosing an approach, it is recommended to consider whether the existing valid statistical procedures allow a satisfactory clinical interpretation. Because alternative methods to deal correctly with multiplicity are often available which may lead to different conclusions, pre-definition of the preferred multiple-level-α-tests is necessary. To avoid problems in interpretation, details of the procedure should be contained in the study protocol or the statistical analysis plan. If a multiple test situation occurs which was not foreseen, a conservative approach will be necessary e.g. Bonferroni’s or a related procedure. Inherently there will be a loss of power. Therefore if a multiple test situation is foreseen pre-specification of the method use to deal with this is recommended This document discusses situations with relevance for multiple testing in clinical trials and commonly practised and acknowledged methods for controlling (or adjusting) type I error. 2.1 Multiple primary variables — when no formal adjustment is needed. The ICH E9 guideline on biostatistical principles in clinical trials recommends that generally clinical trials have one primary variable. A single primary variable is sufficient, if there is a general agreement that a treatment induced change in this variable demonstrates a clinical relevant treatment effect on its own. If, however, a single variable is not sufficient to capture the range of clinically relevant treatment benefits, the use of more than one primary variable may become necessary. Sometimes a series of related objectives is pursued in the same trial each with its own primary variable, and in other cases, a number of primary variables are investigated with the aim of providing convincing evidence of beneficial effects on some, or CPMP/EWPI9O8/99 2/10 ©EMEA 2002 all of them. In these situations planning of the sample size becomes more complex because alternative hypotheses and limits for the power of the single primary variables have to be defined and balanced against each other to give the study a solid basis to meet its objectives. For trials with more than one primary variable the situations described in the following subsections can be distinguished. The methods described allow clinical interpretation, deal satisfactorily with the issue of multiplicity but avoid the need for any formal adjustment of type I error rates. Indeed the methods are members from the set of closed testing procedures that control the family-wise error rate. 2.1.1. Two or more primary variables are needed to describe clinically relevant treatment benefits Statistical signifìcance is needed for all primary variables. Therefore, no formal adjustment is necessary. Here, interpretation of the results is most clear-cut because, in order to provide sufficient evidence of the clinically relevant treatment benefit, each null hypotheses on every primary variable has to be rejected at the same significance level (e.g. 0.05). For examples of this clinical situation, see CPMP Note for Guidance for the treatment of Alzheimer’s disease, or CPMP Points to Consider on clinical investigation of medicinal products in the chronic treatment of patients with chronic obstructive pulmonary disease. In these situations, there is no intention or opportunity to select the most favourable result and, consequently, the individual type I error levels are set equal to the overall type I error level α, i.e. no reduction is necessary. This procedure inflates the relevant type Il error (here: falsely accepting that at least one null hypothesis is true), which in the worst case scenario is the sum of the type II errors connected with the individual hypotheses. This inflation must be taken into account for a proper estimation of the sample size for the trial. 2.1.2. Two or more primary variables ranked according to clinical relevance No formal adjustment is necessary. However, no confirmatory claims can be based on variables that have a rank lower than or equal to that variable whose null hypothesis was the first that could not be rejected. Sometimes a series of related objectives is pursued in the same trial, where one objective is of greatest importance but convincing results in others would clearly add to the value of the treatment. Typical examples are (i) acute effects in depressive disorders followed by prevention of progression (ii) reduction of mortality in acute myocardial infarction followed by prevention of other serious events. In such cases the hypotheses may be tested (and confidence intervals may be provided) according to a hierarchical strategy. The hierarchical order may be a natural one (e.g. hypotheses are ordered in time or with respect to the seriousness of the considered variables) or may result from the particular interests of the investigator. Again, no reduction or splitting of α is necessary. The hierarchical order for testing null hypotheses, however, has to be pre-specified in the study protocol. The effect of such a procedure is that no confirmatory claims can be based on variables that have a rank lower than or equal to that variable whose null hypothesis was the first that could not be rejected. Confidence intervals that are consistent with this hierarchical test procedure can be derived. Evidently, type II errors are inflated for hypotheses that correspond to variables with lower ranks. Note that a similar procedure can be used for dealing with secondary variables (see 3.2). In the literature it is possible to find many methods of dealing with multiple variables that are of value for situations which may, however, be rarely met in confirmatory clinical trials, and CPMP/EWP/908/99 3/10 ©EMEA 2002 which, therefore, are not discussed in this document. Before applying such methods regulatory dialogue is recommended. 2.2 Analysis sets Multiple analyses may be performed on the same variable but with varying subsets of patient data. As is pointed out in the ICH E9 guideline on biostatistical principles for clinical trials, the set of subjects whose data are to be included in the main analyses should be defined in the statistical section of the study protocol. From these sets of subjects one (usually the full set) is selected for the primary analysis. In general, multiple analyses on varying subsets of subjects or with varying measurements for the purpose of investigating the sensitivity of the conclusions drawn from the primary analysis should not be subjected to adjustment for type I error. The main purpose of such analyses is to increase confidence in the results obtained from the primary analysis 2.3 Alternative statistical methods — multiplicity concerns Different statistical models or statistical techniques (e.g. parametric vs. non-parametric or Wilcoxon test versus log rank test) are sometimes tried on the same set of data. Sometimes a two step procedure is applied with the purpose of selecting a particular statistical technique for the main treatment comparison based on the outcome of the first statistical (pre-) test. Multiplicity concerns would immediately arise, if such procedures offered obvious opportunities for selecting a favourable analysis strategy based on knowledge of the patients’ assignment to treatments. There are situations, where selecting the final statistical model based on a formal Blind Review (see ICH E9) is exempted from such concerns. Opportunities for choice in such procedures are often subtle, when these procedures use comparative treatment information, and the influence on the overall type I error is difficult to assess. Finally, the need to change important key features of a study on a post hoc basis may question the credibility of the study and the robustness of the results with the possible consequence that a further study will be necessary. Therefore, such procedures cannot be recommended even when it appears that there is no element of choice. 2.4 Multiplicity in safety variables When a safety variable is part of the confirmatory strategy of a study and thus has a role in the approval or labelling claims, it should not be treated differently from the primary efficacy variables, except for the situation that the observed effects show in the opposite direction and may raise a safety concern (see also 3.3). In the case of adverse effects p-values are of very limited value as substantial differences (expressed as relative risk or risk differences) will raise concern, depending on seriousness, severity or outcome, irrespective of the p-value observed. In those cases where a large number of statistical test procedures is used to serve as a flagging device to signal a potential risk caused by the investigational drug it can generally be stated that an adjustment for multiplicity is counterproductive for considerations of safety. It is clear that in this situation there is no control over the type I error for a single hypothesis and the importance and plausibility of such results will depend on prior knowledge of the pharmacology of the drug. CPMP/EWP/908/99 4/10 ©EMEA 2002 2.5 Multiplicity concern in studies with more than two treatment arms As for studies with more than one primary variable, the proper evaluation and interpretation of a study with more than two treatment arms can become quite complex. This document is not intended to provide an exhaustive discussion of every issue relating to studies with multiple treatment arms, only rarely have these more complex designs been applied in confirmatory clinical trials. Therefore, the following discussion is limited to the more common and simple designs. As a general rule it can be stated that control of the family-wise type I error in the strong sense (i.e. application of closed test procedures) is a minimal prerequisite for confirmatory claims. It should be remembered that the usual confidence intervals for the pairwise differences between treatment groups are — except for a few instances - not consistent with the closed testing procedures, and are usually too narrow. 2.5.1 The three arm ‘gold standard’ design For a disease, where a commonly acknowledged reference drug therapy exists, it is often recommended (when this can be justified on ethical grounds) to demonstrate the efficacy and safety of a new substance in a three arm study with three treatments: the reference drug, placebo and the investigational drug. Usually the aims of such a study are manifold: (I) to demonstrate superiority of the investigational drug over placebo (proof of efficacy); (2) to demonstrate superiority of the reference drug over placebo (proof of assay sensitivity, see ICH E1O, section 2.5.1.1.1); and (3) to demonstrate that the investigational drug retains most of the efficacy of the reference drug as compared to placebo (proof of non-inferiority). If all of these are objectives, all three comparisons must show statistical significance at the required level, and no formal adjustment is necessary. A failure to show the investigational drug as superior to placebo could then be explained either as the investigational drug being not effective (when the reference drug showed superiority over placebo), or as lack of assay sensitivity (when test and reference drug failed to show superiority over placebo). 2.5.2 Proof of efficacy for a fixed combination For fixed combination medicinal products the corresponding CPMP guideline (CPMP/EWP/240/95) requires that ‘each substance of a fixed combination must have documented contribution within the combination’. For a combination with two (mono) components, this requirement has often been interpreted as the need to conduct a study with the two components as mono therapies and the combination therapy in a 3-arm study. Such a study is considered successful, if the combination is shown superior to both components. No formal adjustment of the overall significance level is necessary, because both pairwise comparisons must show statistically significant superiority. Multiple-dose factorial designs are employed for the assessment of combination drugs for the purpose (1) to provide confirmatory evidence that the combination is more effective than either component drug alone (see ICH E4 Note for Guidance on Dose Response Information to support Drug Registration (CPMP/ICH/378/95)), and (2) to identify an effective and safe dose combination (or a range of useful dose combinations) for recommended use in the intended patient population. While (i) usually is achieved using global test strategies, appropriate closed test procedures have to be applied for the purpose of achieving (2). 2.5.3 Dose-response studies For therapeutic dose response studies that aim at identifying one or several doses of an investigational drug for its recommended use in a specific patient population, the control of the family-wise type I error in the strong sense is mandatory. Due to the large variety of design features, assumptions and aims in such studies (e.g. assuming or not assuming monotonicity of the dose response with increasing dose; finding the minimally effective dose under the constrains of the used design; finding a dose that is equivalent (non-inferior) to the CPMP/EWP/908/99 5/10 ©EMEA 2002 recommended dose of a reference drug), specific recommendations are beyond the scope of this document. There are various methods published in the relevant literature on closed test procedures with relevance to multiple dose studies that can be adapted to the specific aims and that provide the necessary control on the type I error. Sometimes a study is not powered sufficiently for the aim to identify and recommend a single effective and safe dose (or a dose range) but is successful only at demonstrating an overall positive correlation of the clinical effect with increasing dose. This is already a valuable achievement (sec ICH E4, section 3.1). Estimates and confidence intervals from pairwise comparisons of single doses are then used in an exploratory manner for the planning of future studies. In this case, an adjustment of the type I error is not necessary. 3. HOW TO INTERPRET SIGNIFICANCE WITH RESPECT TO MULTIPLE SECONDARY VARIABLES AND WHEN CAN A CLAIM BE BASED ON ONE OF THESE? Traditionally, in clinical trial protocols there will be a number of secondary variables for efficacy. Up to now there has been no common consent about the role and the weight of secondary endpoints in clinical trials. 3.1 Variables expressing supportive evidence No claims are intended; confidence intervals and statistical tests are of exploratory nature. Secondary endpoints may provide additional clinical characterisation of treatment effects but are, by themselves, not sufficiently convincing to establish the main evidence in an application for a license or for an additional labelling claim. Here, the inclusion of secondary variables is intended to yield supportive evidence related to the primary objective, and no confirmatory conclusions are needed. Confidence intervals and statistical tests are of exploratory nature and no claims are intended. 3.2 Secondary variables which may become the basis for additional claims Significant effects in these variables can be considered for an additional claim only after the primary objective of the clinical trial has been achieved, and if they were part of the confirmatory strategy More importantly, secondary variables may be related to secondary objectives that become the basis for an additional claim, once the primary objective has been established (see 2.1.2). A valid procedure, to deal with this kind of secondary variable is to proceed hierarchically. Once the null hypothesis concerning the primary objective is rejected (and the primary objective thus established), further confirmatory statistical tests on secondary variables can be performed using a further hierarchical order for the secondary variables themselves if there is more than one. In this case, primary and secondary variables differ just in their place in the hierarchy of hypotheses which, of course, reflects their relative importance in the study. It is of note to mention that changes in secondary variables that are considered a direct consequence of the respective changes in the primary variables cannot be part of the labelling claims. For example, symptoms of depression in schizophrenic patients disappear as patients get into remission from schizophrenia. In this situation, a separate labelling claim on an anti-depressive action of the treatment cannot be made. CPMP/EWP/908/99 6/10 ©EMEA 2002 3.3 Variables indicative of clinical benefit If not defined as primary variables, clinically very important variables (e.g. mortality) need further study when significant benefits are observed, but the primary objective has not been achieved. Variables that have the potential of being indicative of a major clinical benefit or may in a different situation present an important safety issue (e.g. mortality) may be relegated to secondary variables because there is an a priori belief that the size of the planned trial is too small (and thus the power too low) to show a benefit. If, however, the observed beneficial effect is much higher than expected but the study fell short of achieving its primary objective, this would be a typical situation where information from further studies would be needed which can be used in support of the observed beneficial effect. If however, the same variable that may indicate a major clinical benefit exhibits treatment effects in the opposite direction this would give rise to concerns about the safety. A license may then well be refused, regardless of whether or not the variable was embedded in a confirmatory scheme. 4. RELIABLE CONCLUSIONS FROM A SUBGROUP ANALYSIS, AND RESTRICTION OF THE LICENSE TO A SUBGROUP Reliable conclusions from subgroup analyses generally require pre-specification and appropriate statistical analysis strategies. A license may be restricted if unexplained strong heterogeneity is found in important subpopulations, or if heterogeneity of the treatment effect can reasonably be assumed but cannot be sufficiently evaluated for important sub-populations. In clinical trials there are many reasons for examining treatment effects in subgroups. In many studies, subgroup analyses have a supportive or exploratory role after the primary objective has been accomplished, i.e. the demonstration of a significant overall clinical benefit. A specific claim of a beneficial effect in a particular subgroup requires pre-specification of the corresponding null hypothesis and an appropriate confirmatory analysis strategy. It is highly unlikely that claims based on subgroup analyses would be accepted in the absence of a significant effect for the overall study population. Considerations of power would be expected to be covered in the protocol, and randomisation would generally be stratified. The evaluation of uniformity of treatment effects across subgroups is a general regulatory concern. Some factors are known to cause heterogeneity of treatment effects such as gender, age, region, severity of disease, ethnic origin, renal impairment, or differences in absorption or metabolism. Analyses of these important subgroups should be a regular part of the evaluation of a clinical study (when relevant), but should usually be considered exploratory, unless there is a priori suspicion that one or more of these factors may influence the size of effect. However, when a strong interaction is found that indicates an adverse effect of the treatment in one of the subgroups and no convincing explanation for this phenomenon is available or other information confirms the likelihood of an interaction then patients from the respective sub-population may be excluded from the license until additional clinical data are available. This may also apply when there are historical reasons for regulators to believe that a certain sub-population of patients will not benefit from the drug and the results do not strongly contradict this believe. Restriction of a license to certain subgroups is also possible, if a large variety of sub-populations are investigated without proper plans to deal with this situation in the protocol. From the regulatory perspective an overall positive result (statistically and clinically) in the whole study population may not lead to valid claims for all sub-populations if there is a CPMP/EWP/908/99 7/10 ©EMEA 2002 reason to expect heterogeneity of the treatment effect in the respective sub-populations. If a meaningful definition of the overall study population is lacking, licensing may be limited to sub. populations which are adequately represented and in which statistically significant and clinically relevant results were observed. 5. HOW SHOULD ONE INTERPRET THE ANALYSIS OF “RESPONDERS” IN CONJUNCTION WITH THE RAW VARIABLES? If the “responder” analysis is not the primary analysis it may be used after statistical signjficance has been established on the mean level of the required primary variable(s), to establish the clinical relevance of the observed djfferences in the proportion of “responders “. When used in this manner, the test of the null hypothesis of no treatment effect is better carried out on the original primary variable than on the proportion of responders. In a number of applications, for example those concerned with Alzheimer’s disease or epileptic disorders, it is difficult to interpret small but statistically significant improvements in the mean level of the primary variables. For this reason the term “responder” (and “non-responder”) is used to express the clinical benefit of the treatment to individual patients. There may be a number of ways to define a “responder”/“nonresponder”. The definitions should be pre-specified in the protocol and should be clinically convincing. In clinical guidelines, it is stated that the “responder” analysis should be used in establishing the clinical relevance of the observed effect as an aid to assess efficacy and clinical safety. It should be noted that there is some loss of information (and hence loss of statistical power) connected with breaking down the information contained in the original variables unto “responder” and “non-responder”. In some situations, the “responder” criterion may be the primary endpoint (e.g. CPMP guideline on clinical investigation of medicinal products in the treatment of Parkinson’s disease). In this case it should be used to provide the main test of the null hypothesis. However, the situation that is primarily addressed here is when the “responder” analysis is used to show a judgement on clinical relevance, once a statistically significant treatment effect on the mean level of the primary variable(s) loss been established (e.g. CPMP Note for Guidance on clinical investigation of drugs used in weight control, or on the treatment of Alzheimer’s disease). In this case, the results of the “responder” analysis need not be statistically significant but the difference in the proportions of responders should support a statement that the investigated treatment induces clinically relevant effects. It should be noted that a “responder” analysis cannot rescue otherwise disappointing results on the primary variables. 6. HOW SHOULD COMPOSITE VARIABLES BE HANDLED STATISTICALLY WITH RESPECT TO REGULATORY CLAIMS? Usually, the composite variable is primary. All components should be analysed separately. If claims are based on subgroups of components, this needs to be pre-specified and embedded in a valid confirmatory analysis strategy. Treatment should beneficially affect all components, or at least should the clinically more important components not be affected negatively. Any effect of the treatment in one of the components that Is to be reflected in the indication should be clearly supported by the data. There are two types of composite variables. The first type, namely the rating scale, arises as a combination of multiple clinical measurements. With this type there is a longstanding CPMP/EWP/908/99 8/10 ©EMEA 2002 experience of its use in certain indications (e.g. psychiatric or neurological disorders). This type of composite variable is not discussed further in this guideline. The other type of a composite variable arises in the context of survival analysis. Several events are combined to define a composite outcome. A patient is said to have the clinical outcome if s/he suffers from one or more events in a pre-specified list of components (e.g. death, myocardial infarction or disabling stroke). The time to outcome is measured as the time from randomisation of the patient to the first occurrence of any of the events in the list. Usually, the components represent relatively rare events, and to study each component separately would require unmanageably large sample sizes. Composite variables therefore present a means to increase the percentage of patients that reach the clinical outcome, and hence the power of the study. 6.1 The composite variable as the primary endpoint. When a composite variable is used to show efficacy it will usually be the primary endpoint. Therefore, it must meet the requirements for a single primary endpoint, namely that it is capable of providing the key evidence of efficacy that is needed for a license. It is recommended to analyse in addition the single components and clinically relevant groups of components separately, to provide supportive information. There is, however, no need for an adjustment for multiplicity provided significance of the primary endpoint is achieved. If claims are to be based on subgroups of components, this needs to be pre-specified and embedded in a valid confirmatory analysis strategy. 6.2 Treatment should be expected to affect all components in a similar way. When defining a composite variable it is recommended to include only components for which it can be assumed that treatment will influence them similarly. The assumption of similarly directed treatment effects on all components should be based on past experience with studies of similar type. Adding a component that foreseeably is insensitive to treatment effects will lead to an increase in variability, even if it does not affect unbiasedness of the estimation of the treatment difference. A direct consequence would be a decrease in sensitivity for demonstrating superiority between different treatment arms. An increased variance is also a undesirable property in non-inferiority or equivalence studies. Non-inferiority studies will be hard to interpret if negative effects on some components are observed. For studies aiming to show superiority the more general component is preferred as primary endpoint as this is the most conservative analysis. For noninferiority/equivalence studies the more specific component (e.g. disease related mortality) are preferred as primary endpoint for the same reason. 6.3 The clinically more important components should at least not be affected negatively If time to hospitalisation is an endpoint in a clinical study it is not generally appropriate to handle patients as censored who die before they reach the hospital. It is better practice to study a composite endpoint that includes all more important clinical events as components, including death in this example. One concern with composite outcome measures from a regulatory point of view is, however, the possibility that some of the treatments under study may have an adverse effect on one or more of the components, and that this adverse effect is masked by the composite outcome, e.g. by a large beneficial effect on some of the remaining components. This concern is particularly relevant, if the components relate to different degrees of disease severity or clinical importance. For example, if all cause mortality is a component, a separate analysis of all cause mortality should be provided to ensure that there is no adverse effect on this endpoint. Since there is no general agreement how much less then statistical significance in the wrong direction will generate suspicion of an adverse effect, a CPMP/EWP/908/99 9/10 ©EMEA 2002 way to create confidence in support of ‘no adverse effect’, once the data is observed, is to address this issue at the planning stage. For example, the study plan could address the size of the risk of an adverse effect on the more serious components that can be excluded (assuming no treatment difference under the null hypothesis) with a sufficiently high probability, given the planned sample size, and the study report should contain the respective comparative estimates and confidence intervals. 6.4 Any effect of the treatment on one of the components that is to be reflected in the indication should be clearly supported by the data. An important issue for consideration is the claim that can legitimately be made based on a successful primary analysis of a composite endpoint. Difficulties arise if the claims do not properly reflect the fact that a composite endpoint was used, e.g. if a claim is made that explicitly involves a component with the low occurrence. For example, if the composite outcome is ‘death or liver transplantation’ and there are only a few deaths, a claim ‘to reduce mortality and the necessity for liver transplantation’ would not be satisfactory, because in this context the effect on mortality will have a weak basis. This does not mean that one should drop the component ‘death’ from the composite outcome, because the outcome ‘liver transplantation’ would be incomplete without simultaneously considering all disease related outcomes that are at least as serious as ‘liver transplantation’. However, it does mean that different wording should be adopted for the indication, avoiding the implication of an effect on mortality. 7. CONCLUSION In clinical studies it is often necessary to answer more than one question about the efficacy (or safety) of one or more treatments in a specific disease, because the success of a drug development program may depend on a positive answer to more than a single question. It is well known that the chance of a spurious positive chance finding increases with the number of questions posed, if no actions are taken to protect against the inflation of false positive findings from multiple statistical tests. In this context, concern is focused on the opportunity to choose favourable results from multiple analyses. It is therefore necessary that the statistical procedures planned to deal with, or to avoid, multiplicity are fully detailed in the study protocol or in the statistical analysis plan to show an assessment of their suitability and appropriateness. Various different methods have been developed to control the rate of false positive findings. Not all of these methods, however, are equally successful at providing clinically interpretable results and this aspect of the procedure should always be considered. Since estimation of treatment effects is usually an important issue, the availability of confidence intervals connected with a particular procedure may be a criterion for its selection. Additional claims on statistically significant and clinically relevant findings based on secondary variables or on subgroups are possible only after the primary objective of the clinical trial has been achieved, and if the respective questions were pre-specified, and were part of an appropriately planned statistical analysis strategy. CPMP/EWP/908/99 10/10 ©EMEA 2002 INTERNATIONAL CONFERENCE ON HARMONISATION OF TECHNICAL REQUIREMENTS FOR REGISTRATION OF PHARMACEUTICALS FOR HUMAN USE ICH H ARMONISED TRIPARTITE GUIDELINE S TATISTICAL PRINCIPLES FOR CLINICAL TRIALS Recommended for Adoption at Step 4 of the ICH Process on 5 February 1998 by the ICH Steering Committee This Guideline has been developed by the appropriate ICH Expert Working Group and has been subject to consultation by the regulatory parties, in accordance with the ICH Process. At Step 4 of the Process the final draft is recommended for adoption to the regulatory bodies of the European Union, Japan and USA. S TATISTICAL PRINCIPLES FOR CLINICAL TRIALS ICH Harmonised Tripartite Guideline Having reached Step 4 of the ICH Process at the ICH Steering Committee meeting on 5 February 1998, this guideline is recommended for adoption to the three regulatory parties to ICH TABLE OF CONTENTS I. INTRODUCTION ................................ ................................ .............................. 1 1.1 Background and Purpose.............................................................................. 1 1.2 Scope and Direction ...................................................................................... 2 II. CONSIDERATIONS FOR OVERALL CLINICAL DEVELOPMENT ........ 3 2.1 Trial Context................................................................................................. 3 2.1.1 Development Plan ...................................................................... 3 2.1.2 Confirmatory Trial ..................................................................... 4 2.1.3 Exploratory Trial ........................................................................ 4 2.2 Scope of Trials ............................................................................................... 4 2.2.1 Population................................................................................... 4 2.2.2 Primary and Secondary Variables ............................................. 5 2.2.3 Composite Variables ................................................................... 6 2.2.4 Global Assessment Variables ..................................................... 6 2.2.5 Multiple Primary Variables ....................................................... 7 2.2.6 Surrogate Variables .................................................................... 7 2.2.7 Categorised Variables................................................................. 7 2.3 Design Techniques to Avoid Bias ................................................................. 8 III. 2.3.1 Blinding....................................................................................... 8 2.3.2 Randomisation ............................................................................ 9 TRIAL DESIGN CONSIDERATIONS ................................ .......................... 11 3.1 Design Configuration.................................................................................. 11 3.1.1 Parallel Group Design .............................................................. 11 3.1.2 Crossover Design ...................................................................... 11 3.1.3 Factorial Designs ...................................................................... 12 3.2 Multicentre Trials ....................................................................................... 12 3.3 Type of Comparison .................................................................................... 14 3.3.1 Trials to Show Superiority ....................................................... 14 3.3.2 Trials to Show Equivalence or Non-inferiority ........................ 15 3.3.3 Trials to Show Dose-response Relationship ............................. 16 i Statistical Principles for Clinical Trials 3.4 Group Sequential Designs.......................................................................... 16 3.5 Sample Size ................................................................................................ 17 3.6 Data Capture and Processing .................................................................... 18 IV. TRIAL CONDUCT CONSIDERATIONS ................................ ..................... 18 4.1 Trial Monitoring and Interim Analysis ..................................................... 18 4.2 Changes in Inclusion and Exclusion Criteria ............................................ 19 4.3 Accrual Rates.............................................................................................. 19 4.4 Sample Size Adjustment ............................................................................ 19 4.5 Interim Analysis and Early Stopping ........................................................ 20 4.6 Role of Independent Data Monitoring Committee (IDMC) ....................... 21 V. DATA ANALYSIS CONSIDERATI ONS ................................ ....................... 21 5.1 Prespecification of the Analysis ................................................................. 21 5.2 Analysis Sets .............................................................................................. 22 5.2.1 Full Analysis Set ...................................................................... 22 5.2.2 Per Protocol Set........................................................................ 24 5.2.3 Roles of the Different Analysis Sets ........................................ 24 5.3 Missing Values and Outliers ...................................................................... 25 5.4 Data Transformation.................................................................................. 25 5.5 Estimation, Confidence Intervals and Hypothesis Testing ....................... 26 5.6 Adjustment of Significance and Confidence Levels ................................... 26 5.7 Subgroups, Interactions and Covariates ................................................... 27 5.8 Integrity of Data and Computer Software Validity ................................... 27 VI. EVALUATION OF SAFETY AND TOLE RABILITY ................................ .. 28 6.1 Scope of Evaluation .................................................................................... 28 6.2 Choice of Variables and Data Collection .................................................... 28 6.3 Set of Subjects to be Evaluated and Presentation of Data ....................... 28 6.4 Statistical Evaluation................................................................................. 29 6.5 Integrated Summary .................................................................................. 30 VII. REPORTING ................................ ................................ ................................ .. 30 7.1 Evaluation and Reporting .......................................................................... 30 7.2 Summarising the Clinical Database .......................................................... 31 7.2.1 Efficacy Data ............................................................................ 32 7.2.2 Safety Data............................................................................... 32 GLOSSARY ................................ ................................ ................................ .. 33 ii S TATISTICAL PRINCIPLES FOR CLINICAL TRIALS I. INTRODUCTION 1.1 Background and Purpose The efficacy and safety of medicinal products should be demonstrated by clinical trials which follow the guidance in 'Good Clinical Practice: Consolidated Guideline' (ICH E6) adopted by the ICH, 1 May 1996. The role of statistics in clinical trial design and analysis is acknowledged as essential in that ICH guideline. The proliferation of statistical research in the area of clinical trials coupled with the critical role of clinical research in the drug approval process and health care in general necessitate a succinct document on statistical issues related to clinical trials. This guidance is written primarily to attempt to harmonise the principles of statistical methodology applied to clinical trials for marketing applications submitted in Europe, Japan and the United States. As a starting point, this guideline utilised the CPMP (Committee for Proprietary Medicinal Products) Note for Guidance entitled 'Biostatistical Methodology in Clinical Trials in Applications for Marketing Authorisations for Medicinal Products' (December, 1994). It was also influenced by 'Guidelines on the Statistical Analysis of Clinical Studies' (March, 1992) from the Japanese Ministry of Health and Welfare and the U.S. Food and Drug Administration document entitled 'Guideline for the Format and Content of the Clinical and Statistical Sections of a New Drug Application' (July, 1988). Some topics related to statistical principles and methodology are also embedded within other ICH guidelines, particularly those listed below. The specific guidance that contains related text will be identified in various sections of this document. E1A: The Extent of Population Exposure to Assess Clinical Safety E2A: Clinical Safety Data Management: Definitions and Standards for Expedited Reporting E2B: Clinical Safety Data Management: Data Elements for Transmission of Individual Case Safety Reports E2C: Clinical Safety Data Management: Periodic Safety Update Reports for Marketed Drugs E3: Structure and Content of Clinical Study Reports E4: Dose-Response Information to Support Drug Registration E5: Ethnic Factors in the Acceptability of Foreign Clinical Data E6: Good Clinical Practice: Consolidated Guideline E7: Studies in Support of Special Populations: Geriatrics E8: General Considerations for Clinical Trials E10: Choice of Control Group in Clinical Trials M1: Standardisation of Medical Terminology for Regulatory Purposes M3: Non-Clinical Safety Studies for the Conduct of Human Clinical Trials for Pharmaceuticals. 1 Statistical Principles for Clinical Trials This guidance is intended to give direction to sponsors in the design, conduct, analysis, and evaluation of clinical trials of an investigational product in the context of its overall clinical development. The document will also assist scientific experts charged with preparing application summaries or assessing evidence of efficacy and safety, principally from clinical trials in later phases of development. 1.2 Scope and Direction The focus of this guidance is on statistical principles. It does not address the use of specific statistical procedures or methods. Specific procedural steps to ensure that principles are implemented properly are the responsibility of the sponsor. Integration of data across clinical trials is discussed, but is not a primary focus of this guidance. Selected principles and procedures related to data management or clinical trial monitoring activities are covered in other ICH guidelines and are not addressed here. This guidance should be of interest to individuals from a broad range of scientific disciplines. However, it is assumed that the actual responsibility for all statistical work associated with clinical trials will lie with an appropriately qualified and experienced statistician, as indicated in ICH E6. The role and responsibility of the trial statistician (see Glossary), in collaboration with other clinical trial professionals, is to ensure that statistical principles are applied appropriately in clinical trials supporting drug development. Thus, the trial statistician should have a combination of education/training and experience sufficient to implement the principles articulated in this guidance. For each clinical trial contributing to a marketing application, all important details of its design and conduct and the principal features of its proposed statistical analysis should be clearly specified in a protocol written before the trial begins. The extent to which the procedures in the protocol are followed and the primary analysis is planned a priori will contribute to the degree of confidence in the final results and conclusions of the trial. The protocol and subsequent amendments should be approved by the responsible personnel, including the trial statistician. The trial statistician should ensure that the protocol and any amendments cover all relevant statistical issues clearly and accurately, using technical terminology as appropriate. The principles outlined in this guidance are primarily relevant to clinical trials conducted in the later phases of development, many of which are confirmatory trials of efficacy. In addition to efficacy, confirmatory trials may have as their primary variable a safety variable (e.g. an adverse event, a clinical laboratory variable or an electrocardiographic measure), a pharmacodynamic or a pharmacokinetic variable (as in a confirmatory bioequivalence trial). Furthermore, some confirmatory findings may be derived from data integrated across trials, and selected principles in this guidance are applicable in this situation. Finally, although the early phases of drug development consist mainly of clinical trials that are exploratory in nature, statistical principles are also relevant to these clinical trials. Hence, the substance of this document should be applied as far as possible to all phases of clinical development. Many of the principles delineated in this guidance deal with minimising bias (see Glossary) and maximising precision. As used in this guidance, the term 'bias' describes the systematic tendency of any factors associated with the design, conduct, analysis and interpretation of the results of clinical trials to make the estimate of a treatment effect (see Glossary) deviate from its true value. It is important to identify potential sources of bias as completely as possible so that attempts to limit such bias may be made. The presence of bias may seriously compromise the ability to draw valid conclusions from clinical trials. 2 Statistical Principles for Clinical Trials Some sources of bias arise from the design of the trial, for example an assignment of treatments such that subjects at lower risk are systematically assigned to one treatment. Other sources of bias arise during the conduct and analysis of a clinical trial. For example, protocol violations and exclusion of subjects from analysis based upon knowledge of subject outcomes are possible sources of bias that may affect the accurate assessment of the treatment effect. Because bias can occur in subtle or unknown ways and its effect is not measurable directly, it is important to evaluate the robustness of the results and primary conclusions of the trial. Robustness is a concept that refers to the sensitivity of the overall conclusions to various limitations of the data, assumptions, and analytic approaches to data analysis. Robustness implies that the treatment effect and primary conclusions of the trial are not substantially affected when analyses are carried out based on alternative assumptions or analytic approaches. The interpretation of statistical measures of uncertainty of the treatment effect and treatment comparisons should involve consideration of the potential contribution of bias to the p-value, confidence interval, or inference. Because the predominant approaches to the design and analysis of clinical trials have been based on frequentist statistical methods, the guidance largely refers to the use of frequentist methods (see Glossary) when discussing hypothesis testing and/or confidence intervals. This should not be taken to imply that other approaches are not appropriate: the use of Bayesian (see Glossary) and other approaches may be considered when the reasons for their use are clear and when the resulting conclusions are sufficiently robust. II. CONSIDERATIONS FOR OVERALL CLINICAL DEVELOPMENT 2.1 Trial Context 2.1.1 Development Plan The broad aim of the process of clinical development of a new drug is to find out whether there is a dose range and schedule at which the drug can be shown to be simultaneously safe and effective, to the extent that the risk-benefit relationship is acceptable. The particular subjects who may benefit from the drug, and the specific indications for its use, also need to be defined. Satisfying these broad aims usually requires an ordered programme of clinical trials, each with its own specific objectives (see ICH E8). This should be specified in a clinical plan, or a series of plans, with appropriate decision points and flexibility to allow modification as knowledge accumulates. A marketing application should clearly describe the main content of such plans, and the contribution made by each trial. Interpretation and assessment of the evidence from the total programme of trials involves synthesis of the evidence from the individual trials (see Section 7.2). This is facilitated by ensuring that common standards are adopted for a number of features of the trials such as dictionaries of medical terms, definition and timing of the main measurements, handling of protocol deviations and so on. A statistical summary, overview or meta-analysis (see Glossary) may be informative when medical questions are addressed in more than one trial. Where possible this should be envisaged in the plan so that the relevant trials are clearly identified and any necessary common features of their designs are specified in advance. Other major statistical issues (if any) that are expected to affect a number of trials in a common plan should be addressed in that plan. 2.1.2 Confirmatory Trial 3 Statistical Principles for Clinical Trials A confirmatory trial is an adequately controlled trial in which the hypotheses are stated in advance and evaluated. As a rule, confirmatory trials are necessary to provide firm evidence of efficacy or safety. In such trials the key hypothesis of interest follows directly from the trial’s primary objective, is always pre-defined, and is the hypothesis that is subsequently tested when the trial is complete. In a confirmatory trial it is equally important to estimate with due precision the size of the effects attributable to the treatment of interest and to relate these effects to their clinical significance. Confirmatory trials are intended to provide firm evidence in support of claims and hence adherence to protocols and standard operating procedures is particularly important; unavoidable changes should be explained and documented, and their effect examined. A justification of the design of each such trial, and of other important statistical aspects such as the principal features of the planned analysis, should be set out in the protocol. Each trial should address only a limited number of questions. Firm evidence in support of claims requires that the results of the confirmatory trials demonstrate that the investigational product under test has clinical benefits. The confirmatory trials should therefore be sufficient to answer each key clinical question relevant to the efficacy or safety claim clearly and definitively. In addition, it is important that the basis for generalisation (see Glossary) to the intended patient population is understood and explained; this may also influence the number and type (e.g. specialist or general practitioner) of centres and/or trials needed. The results of the confirmatory trial(s) should be robust. In some circumstances the weight of evidence from a single confirmatory trial may be sufficient. 2.1.3 Exploratory Trial The rationale and design of confirmatory trials nearly always rests on earlier clinical work carried out in a series of exploratory studies. Like all clinical trials, these exploratory studies should have clear and precise objectives. However, in contrast to confirmatory trials, their objectives may not always lead to simple tests of pre-defined hypotheses. In addition, exploratory trials may sometimes require a more flexible approach to design so that changes can be made in response to accumulating results. Their analysis may entail data exploration; tests of hypothesis may be carried out, but the choice of hypothesis may be data dependent. Such trials cannot be the basis of the formal proof of efficacy, although they may contribute to the total body of relevant evidence. Any individual trial may have both confirmatory and exploratory aspects. For example, in most confirmatory trials the data are also subjected to exploratory analyses which serve as a basis for explaining or supporting their findings and for suggesting further hypotheses for later research. The protocol should make a clear distinction between the aspects of a trial which will be used for confirmatory proof and the aspects which will provide data for exploratory analysis. 2.2 Scope of Trials 2.2.1 Population In the earlier phases of drug development the choice of subjects for a clinical trial may be heavily influenced by the wish to maximise the chance of observing specific clinical effects of interest, and hence they may come from a very narrow subgroup of the total patient population for which the drug may eventually be indicated. However by the time the confirmatory trials are undertaken, the subjects in the trials should more closely mirror the target population. Hence, in these trials it is generally helpful to relax the inclusion and exclusion criteria as much as possible within the target 4 Statistical Principles for Clinical Trials population, while maintaining sufficient homogeneity to permit precise estimation of treatment effects. No individual clinical trial can be expected to be totally representative of future users, because of the possible influences of geographical location, the time when it is conducted, the medical practices of the particular investigator(s) and clinics, and so on. However the influence of such factors should be reduced wherever possible, and subsequently discussed during the interpretation of the trial results. 2.2.2 Primary and S econdary Variables The primary variable (‘target’ variable, primary endpoint) should be the variable capable of providing the most clinically relevant and convincing evidence directly related to the primary objective of the trial. There should generally be only one primary variable. This will usually be an efficacy variable, because the primary objective of most confirmatory trials is to provide strong scientific evidence regarding efficacy. Safety/tolerability may sometimes be the primary variable, and will always be an important consideration. Measurements relating to quality of life and health economics are further potential primary variables. The selection of the primary variable should reflect the accepted norms and standards in the relevant field of research. The use of a reliable and validated variable with which experience has been gained either in earlier studies or in published literature is recommended. There should be sufficient evidence that the primary variable can provide a valid and reliable measure of some clinically relevant and important treatment benefit in the patient population described by the inclusion and exclusion criteria. The primary variable should generally be the one used when estimating the sample size (see section 3.5). In many cases, the approach to assessing subject outcome may not be straightforward and should be carefully defined. For example, it is inadequate to specify mortality as a primary variable without further clarification; mortality may be assessed by comparing proportions alive at fixed points in time, or by comparing overall distributions of survival times over a specified interval. Another common example is a recurring event; the measure of treatment effect may again be a simple dichotomous variable (any occurrence during a specified interval), time to first occurrence, rate of occurrence (events per time units of observation), etc. The assessment of functional status over time in studying treatment for chronic disease presents other challenges in selection of the primary variable. There are many possible approaches, such as comparisons of the assessments done at the beginning and end of the interval of observation, comparisons of slopes calculated from all assessments throughout the interval, comparisons of the proportions of subjects exceeding or declining beyond a specified threshold, or comparisons based on methods for repeated measures data. To avoid multiplicity concerns arising from post hoc definitions, it is critical to specify in the protocol the precise definition of the primary variable as it will be used in the statistical analysis. In addition, the clinical relevance of the specific primary variable selected and the validity of the associated measurement procedures will generally need to be addressed and justified in the protocol. The primary variable should be specified in the protocol, along with the rationale for its selection. Redefinition of the primary variable after unblinding will almost always be unacceptable, since the biases this introduces are difficult to assess. When the clinical effect defined by the primary objective is to be measured in more than one way, the protocol should identify one of the measurements as the primary variable on the basis of clinical relevance, importance, objectivity, and/or other relevant characteristics, whenever such selection is feasible. 5 Statistical Principles for Clinical Trials Secondary variables are either supportive measurements related to the primary objective or measurements of effects related to the secondary objectives. Their predefinition in the protocol is also important, as well as an explanation of their relative importance and roles in interpretation of trial results. The number of secondary variables should be limited and should be related to the limited number of questions to be answered in the trial. 2.2.3 Composite Variables If a single primary variable cannot be selected from multiple measurements associated with the primary objective, another useful strategy is to integrate or combine the multiple measurements into a single or 'composite' variable, using a predefined algorithm. Indeed, the primary variable sometimes arises as a combination of multiple clinical measurements (e.g. the rating scales used in arthritis, psychiatric disorders and elsewhere). This approach addresses the multiplicity problem without requiring adjustment to the type I error. The method of combining the multiple measurements should be specified in the protocol, and an interpretation of the resulting scale should be provided in terms of the size of a clinically relevant benefit. When a composite variable is used as a primary variable, the components of this variable may sometimes be analysed separately, where clinically meaningful and validated. When a rating scale is used as a primary variable, it is especially important to address such factors as content validity (see Glossary), inter- and intra-rater reliability (see Glossary) and responsiveness for detecting changes in the severity of disease. 2.2.4 Global Assessment Variables In some cases, 'global assessment' variables (see Glossary) are developed to measure the overall safety, overall efficacy, and/or overall usefulness of a treatment. This type of variable integrates objective variables and the investigator’s overall impression about the state or change in the state of the subject, and is usually a scale of ordered categorical ratings. Global assessments of overall efficacy are well established in some therapeutic areas, such as neurology and psychiatry. Global assessment variables generally have a subjective component. When a global assessment variable is used as a primary or secondary variable, fuller details of the scale should be included in the protocol with respect to: 1) the relevance of the scale to the primary objective of the trial; 2) the basis for the validity and reliability of the scale; 3) how to utilise the data collected on an individual subject to assign him/her to a unique category of the scale; 4) how to assign subjects with missing data to a unique category of the scale, or otherwise evaluate them. If objective variables are considered by the investigator when making a global assessment, then those objective variables should be considered as additional primary, or at least important secondary, variables. Global assessment of usefulness integrates components of both benefit and risk and reflects the decision making process of the treating physician, who must weigh benefit and risk in making product use decisions. A problem with global usefulness variables is that their use could in some cases lead to the result of two products being declared equivalent despite having very different profiles of beneficial and adverse effects. For example, judging the global usefulness of a treatment as equivalent or superior to an 6 Statistical Principles for Clinical Trials alternative may mask the fact that it has little or no efficacy but fewer adverse effects. Therefore it is not advisable to use a global usefulness variable as a primary variable. If global usefulness is specified as primary, it is important to consider specific efficacy and safety outcomes separately as additional primary variables. 2.2.5 Multiple Primary Variables It may sometimes be desirable to use more than one primary variable, each of which (or a subset of which) could be sufficient to cover the range of effects of the therapies. The planned manner of interpretation of this type of evidence should be carefully spelled out. It should be clear whether an impact on any of the variables, some minimum number of them, or all of them, would be considered necessary to achieve the trial objectives. The primary hypothesis or hypotheses and parameters of interest (e.g. mean, percentage, distribution) should be clearly stated with respect to the primary variables identified, and the approach to statistical inference described. The effect on the type I error should be explained because of the potential for multiplicity problems (see Section 5.6); the method of controlling type I error should be given in the protocol. The extent of intercorrelation among the proposed primary variables may be considered in evaluating the impact on type I error. If the purpose of the trial is to demonstrate effects on all of the designated primary variables, then there is no need for adjustment of the type I error, but the impact on type II error and sample size should be carefully considered. 2.2.6 Surrogate Variables When direct assessment of the clinical benefit to the subject through observing actual clinical efficacy is not practical, indirect criteria (surrogate variables - see Glossary) may be considered. Commonly accepted surrogate variables are used in a number of indications where they are believed to be reliable predictors of clinical benefit. There are two principal concerns with the introduction of any proposed surrogate variable. First, it may not be a true predictor of the clinical outcome of interest. For example it may measure treatment activity associated with one specific pharmacological mechanism, but may not provide full information on the range of actions and ultimate effects of the treatment, whether positive or negative. There have been many instances where treatments showing a highly positive effect on a proposed surrogate have ultimately been shown to be detrimental to the subjects' clinical outcome; conversely, there are cases of treatments conferring clinical benefit without measurable impact on proposed surrogates. Secondly, proposed surrogate variables may not yield a quantitative measure of clinical benefit that can be weighed directly against adverse effects. Statistical criteria for validating surrogate variables have been proposed but the experience with their use is relatively limited. In practice, the strength of the evidence for surrogacy depends upon (i) the biological plausibility of the relationship, (ii) the demonstration in epidemiological studies of the prognostic value of the surrogate for the clinical outcome and (iii) evidence from clinical trials that treatment effects on the surrogate correspond to effects on the clinical outcome. Relationships between clinical and surrogate variables for one product do not necessarily apply to a product with a different mode of action for treating the same disease. 2.2.7 Categorised Variables Dichotomisation or other categorisation of continuous or ordinal variables may sometimes be desirable. Criteria of 'success' and 'response' are common examples of dichotomies which require precise specification in terms of, for example, a minimum percentage improvement (relative to baseline) in a continuous variable, or a ranking categorised as at or above some threshold level (e.g., 'good') on an ordinal rating scale. 7 Statistical Principles for Clinical Trials The reduction of diastolic blood pressure below 90mmHg is a common dichotomisation. Categorisations are most useful when they have clear clinical relevance. The criteria for categorisation should be pre-defined and specified in the protocol, as knowledge of trial results could easily bias the choice of such criteria. Because categorisation normally implies a loss of information, a consequence will be a loss of power in the analysis; this should be accounted for in the sample size calculation. 2.3 Design Techniques to Avoid Bias The most important design techniques for avoiding bias in clinical trials are blinding and randomisation, and these should be normal features of most controlled clinical trials intended to be included in a marketing application. Most such trials follow a double-blind approach in which treatments are pre-packed in accordance with a suitable randomisation schedule, and supplied to the trial centre(s) labelled only with the subject number and the treatment period so that no one involved in the conduct of the trial is aware of the specific treatment allocated to any particular subject, not even as a code letter. This approach will be assumed in Section 2.3.1 and most of Section 2.3.2, exceptions being considered at the end. Bias can also be reduced at the design stage by specifying procedures in the protocol aimed at minimising any anticipated irregularities in trial conduct that might impair a satisfactory analysis, including various types of protocol violations, withdrawals and missing values. The protocol should consider ways both to reduce the frequency of such problems, and also to handle the problems that do occur in the analysis of data. 2.3.1 Blinding Blinding or masking is intended to limit the occurrence of conscious and unconscious bias in the conduct and interpretation of a clinical trial arising from the influence which the knowledge of treatment may have on the recruitment and allocation of subjects, their subsequent care, the attitudes of subjects to the treatments, the assessment of end-points, the handling of withdrawals, the exclusion of data from analysis, and so on. The essential aim is to prevent identification of the treatments until all such opportunities for bias have passed. A double-blind trial is one in which neither the subject nor any of the investigator or sponsor staff who are involved in the treatment or clinical evaluation of the subjects are aware of the treatment received. This includes anyone determining subject eligibility, evaluating endpoints, or assessing compliance with the protocol. This level of blinding is maintained throughout the conduct of the trial, and only when the data are cleaned to an acceptable level of quality will appropriate personnel be unblinded. If any of the sponsor staff who are not involved in the treatment or clinical evaluation of the subjects are required to be unblinded to the treatment code (e.g. bioanalytical scientists, auditors, those involved in serious adverse event reporting), the sponsor should have adequate standard operating procedures to guard against inappropriate dissemination of treatment codes. In a single-blind trial the investigator and/or his staff are aware of the treatment but the subject is not, or vice versa. In an open-label trial the identity of treatment is known to all. The double-blind trial is the optimal approach. This requires that the treatments to be applied during the trial cannot be distinguished (appearance, taste, etc.) either before or during administration, and that the blind is maintained appropriately during the whole trial. Difficulties in achieving the double-blind ideal can arise: the treatments may be of a completely different nature, for example, surgery and drug therapy; two drugs may have different formulations and, although they could be made indistinguishable by the use of capsules, changing the formulation might also change the pharmacokinetic 8 Statistical Principles for Clinical Trials and/or pharmacodynamic properties and hence require that bioequivalence of the formulations 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 'double-dummy' (see Glossary) technique. This technique may sometimes force an administration scheme that is sufficiently unusual to influence adversely the motivation and compliance of the subjects. Ethical difficulties may also interfere with its use when, for example, it entails dummy operative procedures. Nevertheless, extensive efforts should be made to overcome these difficulties. The double-blind nature of some clinical trials may be partially compromised by apparent treatment induced effects. In such cases, blinding may be improved by blinding investigators and relevant sponsor staff to certain test results (e.g. selected clinical laboratory measures). Similar approaches (see below) to minimising bias in open-label trials should be considered in trials where unique or specific treatment effects may lead to unblinding individual patients. 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. Single-blind and open-label trials provide additional flexibility, but it is particularly important that the investigator's knowledge of the next treatment should not influence the decision to enter the subject; this decision should precede knowledge of the randomised treatment. For these trials, consideration should be given to the use of a centralised randomisation method, such as telephone randomisation, to administer the assignment of randomised treatment. In addition, clinical assessments should be made by medical staff who are not involved in treating the subjects and who remain blind to treatment. In single-blind or open-label trials every effort should be made to minimise the various known sources of bias and primary variables should be as objective as possible. The reasons for the degree of blinding adopted should be explained in the protocol, together with steps taken to minimise bias by other means. For example, the sponsor should have adequate standard operating procedures to ensure that access to the treatment code is appropriately restricted during the process of cleaning the database prior to its release for analysis. Breaking the blind (for a single subject) should be considered only when knowledge of the treatment assignment is deemed essential by the subject’s physician for the subject’s care. Any intentional or unintentional breaking of the blind should be reported and explained at the end of the trial, irrespective of the reason for its occurrence. The procedure and timing for revealing the treatment assignments should be documented. In this document, the blind review (see Glossary) of data refers to the checking of data during the period of time between trial completion (the last observation on the last subject) and the breaking of the blind. 2.3.2 Randomisation Randomisation introduces a deliberate element of chance into the assignment of treatments to subjects in a clinical trial. During subsequent analysis of the trial data, it provides a sound statistical basis for the quantitative evaluation of the evidence relating to treatment effects. It also tends to produce treatment groups in which the distributions of prognostic factors, known and unknown, are similar. In combination with blinding, randomisation helps to avoid possible bias in the selection and allocation of subjects arising from the predictability of treatment assignments. The randomisation schedule of a clinical trial documents the random allocation of treatments to subjects. In the simplest situation it is a sequential list of treatments (or treatment sequences in a crossover trial) or corresponding codes by subject 9 Statistical Principles for Clinical Trials number. The logistics of some trials, such as those with a screening phase, may make matters more complicated, but the unique pre-planned assignment of treatment, or treatment sequence, to subject should be clear. Different trial designs will require different procedures for generating randomisation schedules. The randomisation schedule should be reproducible (if the need arises). Although unrestricted randomisation is an acceptable approach, some advantages can generally be gained by randomising subjects in blocks. This helps to increase the comparability of the treatment groups, particularly when subject characteristics may change over time, as a result, for example, of changes in recruitment policy. It also provides a better guarantee that the treatment groups will be of nearly equal size. In crossover trials it provides the means of obtaining balanced designs with their greater efficiency and easier interpretation. Care should be taken to choose block lengths that are sufficiently short to limit possible imbalance, but that are long enough to avoid predictability towards the end of the sequence in a block. Investigators and other relevant staff should generally be blind to the block length; the use of two or more block lengths, randomly selected for each block, can achieve the same purpose. (Theoretically, in a double-blind trial predictability does not matter, but the pharmacological effects of drugs may provide the opportunity for intelligent guesswork.) In multicentre trials (see Glossary) the randomisation procedures should be organised centrally. It is advisable to have a separate random scheme for each centre, i.e. to stratify by centre or to allocate several whole blocks to each 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 balanced allocation within strata; this has greater potential benefit in small trials. The use of more than two or three stratification factors is rarely necessary, is less successful at achieving balance and is logistically troublesome. The use of a dynamic allocation procedure (see below) may help to achieve balance across a number of stratification factors simultaneously provided the rest of the trial procedures can be adjusted to accommodate an approach of this type. Factors on which randomisation has been stratified should be accounted for later in the analysis. The next subject to be randomised into a trial should always receive the treatment corresponding to the next free number in the appropriate randomisation schedule (in the respective stratum, if randomisation is stratified). The appropriate number and associated treatment for the next subject should only be allocated when entry of that subject to the randomised part of the trial has been confirmed. Details of the randomisation that facilitate predictability (e.g. block length) should not be contained in the trial protocol. The randomisation schedule itself should be filed securely by the sponsor or an independent party in a manner that ensures that blindness is properly maintained throughout the trial. Access to the randomisation schedule during the trial should take into account the possibility that, in an emergency, the blind may have to be broken for any subject. The procedure to be followed, the necessary documentation, and the subsequent treatment and assessment of the subject should all be described in the protocol. Dynamic allocation is an alternative procedure in which the allocation of treatment to a subject is influenced by the current balance of allocated treatments and, in a stratified trial, by the stratum to which the subject belongs and the balance within that stratum. Deterministic dynamic allocation procedures should be avoided and an appropriate element of randomisation should be incorporated for each treatment allocation. Every effort should be made to retain the double-blind status of the trial. For example, knowledge of the treatment code may be restricted to a central trial office from where the dynamic allocation is controlled, generally through telephone 10 Statistical Principles for Clinical Trials contact. This in turn permits additional checks of eligibility criteria and establishes entry into the trial, features that can be valuable in certain types of multicentre trial. The usual system of pre-packing and labelling drug supplies for double-blind trials can then be followed, but the order of their use is no longer sequential. It is desirable to use appropriate computer algorithms to keep personnel at the central trial office blind to the treatment code. The complexity of the logistics and potential impact on the analysis should be carefully evaluated when considering dynamic allocation. III. TRIAL DESIGN CONSIDERATIONS 3.1 Design Configuration 3.1.1 Parallel Group Design The most common clinical trial design for confirmatory trials is the parallel group design in which subjects are randomised to one of two or more arms, each arm being allocated a different treatment. These treatments will include the investigational product at one or more doses, and one or more control treatments, such as placebo and/or an active comparator. The assumptions underlying this design are less complex than for most other designs. However, as with other designs, there may be additional features of the trial that complicate the analysis and interpretation (e.g. covariates, repeated measurements over time, interactions between design factors, protocol violations, dropouts (see Glossary) and withdrawals). 3.1.2 Crossover Design In the crossover design, each subject is randomised to a sequence of two or more treatments, and hence acts as his own control for treatment comparisons. This simple manoeuvre is attractive primarily because it reduces the number of subjects and usually the number of assessments needed to achieve a specific power, sometimes to a marked extent. In the simplest 2×2 crossover design each subject receives each of two treatments in randomised order in two successive treatment periods, often separated by a washout period. The most common extension of this entails comparing n(>2) treatments in n periods, each subject receiving all n treatments. Numerous variations exist, such as designs in which each subject receives a subset of n(>2) treatments, or ones in which treatments are repeated within a subject. Crossover designs have a number of problems that can invalidate their results. The chief difficulty concerns carryover, that is, the residual influence of treatments in subsequent treatment periods. In an additive model the effect of unequal carryover will be to bias direct treatment comparisons. In the 2×2 design the carryover effect cannot be statistically distinguished from the interaction between treatment and period and the test for either of these effects lacks power because the corresponding contrast is 'between subject'. This problem is less acute in higher order designs, but cannot be entirely dismissed. When the crossover design is used it is therefore important to avoid carryover. This is best done by selective and careful use of the design on the basis of adequate knowledge of both the disease area and the new medication. The disease under study should be chronic and stable. The relevant effects of the medication should develop fully within the treatment period. The washout periods should be sufficiently long for complete reversibility of drug effect. The fact that these conditions are likely to be met should be established in advance of the trial by means of prior information and data. There are additional problems that need careful attention in crossover trials. The most notable of these are the complications of analysis and interpretation arising from the loss of subjects. Also, the potential for carryover leads to difficulties in assigning adverse events which occur in later treatment periods to the appropriate 11 Statistical Principles for Clinical Trials treatment. These, and other issues, are described in ICH E4. The crossover design should generally be restricted to situations where losses of subjects from the trial are expected to be small. A common, and generally satisfactory, use of the 2×2 crossover design is to demonstrate the bioequivalence of two formulations of the same medication. In this particular application in healthy volunteers, carryover effects on the relevant pharmacokinetic variable are most unlikely to occur if the wash-out time between the two periods is sufficiently long. However it is still important to check this assumption during analysis on the basis of the data obtained, for example by demonstrating that no drug is detectable at the start of each period. 3.1.3 Factorial Designs In a factorial design two or more treatments are evaluated simultaneously through the use of varying combinations of the treatments. The simplest example is the 2×2 factorial design in which subjects are randomly allocated to one of the four possible combinations of two treatments, A and B say. These are: A alone; B alone; both A and B; neither A nor B. In many cases this design is used for the specific purpose of examining the interaction of A and B. The statistical test of interaction may lack power to detect an interaction if the sample size was calculated based on the test for main effects. This consideration is important when this design is used for examining the joint effects of A and B, in particular, if the treatments are likely to be used together. Another important use of the factorial design is to establish the dose-response characteristics of the simultaneous use of treatments C and D, especially when the efficacy of each monotherapy has been established at some dose in prior trials. A number, m, of doses of C is selected, usually including a zero dose (placebo), and a similar number, n, of doses of D. The full design then consists of m×n treatment groups, each receiving a different combination of doses of C and D. The resulting estimate of the response surface may then be used to help to identify an appropriate combination of doses of C and D for clinical use (see ICH E4). In some cases, the 2×2 design may be used to make efficient use of clinical trial subjects by evaluating the efficacy of the two treatments with the same number of subjects as would be required to evaluate the efficacy of either one alone. This strategy has proved to be particularly valuable for very large mortality trials. The efficiency and validity of this approach depends upon the absence of interaction between treatments A and B so that the effects of A and B on the primary efficacy variables follow an additive model, and hence the effect of A is virtually identical whether or not it is additional to the effect of B. As for the crossover trial, evidence that this condition is likely to be met should be established in advance of the trial by means of prior information and data. 3.2 Multicentre Trials Multicentre trials are carried out for two main reasons. Firstly, a multicentre trial is an accepted way of evaluating a new medication more efficiently; under some circumstances, it may present the only practical means of accruing sufficient subjects to satisfy the trial objective within a reasonable time-frame. Multicentre trials of this nature may, in principle, be carried out at any stage of clinical development. They may have several centres with a large number of subjects per centre or, in the case of a rare disease, they may have a large number of centres with very few subjects per centre. Secondly, a trial may be designed as a multicentre (and multi-investigator) trial primarily to provide a better basis for the subsequent generalisation of its findings. 12 Statistical Principles for Clinical Trials This arises from the possibility of recruiting the subjects from a wider population and of administering the medication in a broader range of clinical settings, thus presenting an experimental situation that is more typical of future use. In this case the involvement of a number of investigators also gives the potential for a wider range of clinical judgement concerning the value of the medication. Such a trial would be a confirmatory trial in the later phases of drug development and would be likely to involve a large number of investigators and centres. It might sometimes be conducted in a number of different countries in order to facilitate generalisability (see Glossary) even further. If a multicentre trial is to be meaningfully interpreted and extrapolated, then the manner in which the protocol is implemented should be clear and similar at all centres. Furthermore the usual sample size and power calculations depend upon the assumption that the differences between the compared treatments in the centres are unbiased estimates of the same quantity. It is important to design the common protocol and to conduct the trial with this background in mind. Procedures should be standardised as completely as possible. Variation of evaluation criteria and schemes can be reduced by investigator meetings, by the training of personnel in advance of the trial and by careful monitoring during the trial. Good design should generally aim to achieve the same distribution of subjects to treatments within each centre and good management should maintain this design objective. Trials that avoid excessive variation in the numbers of subjects per centre and trials that avoid a few very small centres have advantages if it is later found necessary to take into account the heterogeneity of the treatment effect from centre to centre, because they reduce the differences between different weighted estimates of the treatment effect. (This point does not apply to trials in which all centres are very small and in which centre does not feature in the analysis.) Failure to take these precautions, combined with doubts about the homogeneity of the results may, in severe cases, reduce the value of a multicentre trial to such a degree that it cannot be regarded as giving convincing evidence for the sponsor’s claims. In the simplest multicentre trial, each investigator will be responsible for the subjects recruited at one hospital, so that ‘centre’ is identified uniquely by either investigator or hospital. In many trials, however, the situation is more complex. One investigator may recruit subjects from several hospitals; one investigator may represent a team of clinicians (subinvestigators) who all recruit subjects from their own clinics at one hospital or at several associated hospitals. Whenever there is room for doubt about the definition of centre in a statistical model, the statistical section of the protocol (see Section 5.1) should clearly define the term (e.g. by investigator, location or region) in the context of the particular trial. In most instances centres can be satisfactorily defined through the investigators and ICH E6 provides relevant guidance in this respect. In cases of doubt the aim should be to define centres so as to achieve homogeneity in the important factors affecting the measurements of the primary variables and the influence of the treatments. Any rules for combining centres in the analysis should be justified and specified prospectively in the protocol where possible, but in any case decisions concerning this approach should always be taken blind to treatment, for example at the time of the blind review. The statistical model to be adopted for the estimation and testing of treatment effects should be described in the protocol. The main treatment effect may be investigated first using a model which allows for centre differences, but does not include a term for treatment-by-centre interaction. If the treatment effect is homogeneous across centres, the routine inclusion of interaction terms in the model reduces the efficiency of the test for the main effects. In the presence of true heterogeneity of treatment effects, the interpretation of the main treatment effect is controversial. 13 Statistical Principles for Clinical Trials In some trials, for example some large mortality trials with very few subjects per centre, there may be no reason to expect the centres to have any influence on the primary or secondary variables because they are unlikely to represent influences of clinical importance. In other trials it may be recognised from the start that the limited numbers of subjects per centre will make it impracticable to include the centre effects in the statistical model. In these cases it is not appropriate to include a term for centre in the model, and it is not necessary to stratify the randomisation by centre in this situation. If positive treatment effects are found in a trial with appreciable numbers of subjects per centre, there should generally be an exploration of the heterogeneity of treatment effects across centres, as this may affect the generalisability of the conclusions. Marked heterogeneity may be identified by graphical display of the results of individual centres or by analytical methods, such as a significance test of the treatment-by-centre interaction. When using such a statistical significance test, it is important to recognise that this generally has low power in a trial designed to detect the main effect of treatment. If heterogeneity of treatment effects is found, this should be interpreted with care and vigorous attempts should be made to find an explanation in terms of other features of trial management or subject characteristics. Such an explanation will usually suggest appropriate further analysis and interpretation. In the absence of an explanation, heterogeneity of treatment effect as evidenced, for example, by marked quantitative interactions (see Glossary) implies that alternative estimates of the treatment effect may be required, giving different weights to the centres, in order to substantiate the robustness of the estimates of treatment effect. It is even more important to understand the basis of any heterogeneity characterised by marked qualitative interactions (see Glossary), and failure to find an explanation may necessitate further clinical trials before the treatment effect can be reliably predicted. Up to this point the discussion of multicentre trials has been based on the use of fixed effect models. Mixed models may also be used to explore the heterogeneity of the treatment effect. These models consider centre and treatment-by-centre effects to be random, and are especially relevant when the number of sites is large. 3.3 Type of Comparison 3.3.1 Trials to Show Superiority Scientifically, efficacy is most convincingly established by demonstrating superiority to placebo in a placebo-controlled trial, by showing superiority to an active control treatment or by demonstrating a dose-response relationship. This type of trial is referred to as a ‘superiority’ trial (see Glossary). Generally in this guidance superiority trials are assumed, unless it is explicitly stated otherwise. For serious illnesses, when a therapeutic treatment which has been shown to be efficacious by superiority trial(s) exists, a placebo-controlled trial may be considered unethical. In that case the scientifically sound use of an active treatment as a control should be considered. The appropriateness of placebo control vs. active control should be considered on a trial by trial basis. 3.3.2 Trials to Show Equivalence or Non-inferiority In some cases, an investigational product is compared to a reference treatment without the objective of showing superiority. This type of trial is divided into two major categories according to its objective; one is an 'equivalence' trial (see Glossary) and the other is a 'non-inferiority' trial (see Glossary). 14 Statistical Principles for Clinical Trials Bioequivalence trials fall into the former category. In some situations, clinical equivalence trials are also undertaken for other regulatory reasons such as demonstrating the clinical equivalence of a generic product to the marketed product when the compound is not absorbed and therefore not present in the blood stream. Many active control trials are designed to show that the efficacy of an investigational product is no worse than that of the active comparator, and hence fall into the latter category. Another possibility is a trial in which multiple doses of the investigational drug are compared with the recommended dose or multiple doses of the standard drug. The purpose of this design is simultaneously to show a dose-response relationship for the investigational product and to compare the investigational product with the active control. Active control equivalence or non-inferiority trials may also incorporate a placebo, thus pursuing multiple goals in one trial; for example, they may establish superiority to placebo and hence validate the trial design and simultaneously evaluate the degree of similarity of efficacy and safety to the active comparator. There are well known difficulties associated with the use of the active control equivalence (or non-inferiority) trials that do not incorporate a placebo or do not use multiple doses of the new drug. These relate to the implicit lack of any measure of internal validity (in contrast to superiority trials), thus making external validation necessary. The equivalence (or non-inferiority) trial is not conservative in nature, so that many flaws in the design or conduct of the trial will tend to bias the results towards a conclusion of equivalence. For these reasons, the design features of such trials should receive special attention and their conduct needs special care. For example, it is especially important to minimise the incidence of violations of the entry criteria, non-compliance, withdrawals, losses to follow-up, missing data and other deviations from the protocol, and also to minimise their impact on the subsequent analyses. Active comparators should be chosen with care. An example of a suitable active comparator would be a widely used therapy whose efficacy in the relevant indication has been clearly established and quantified in well designed and well documented superiority trial(s) and which can be reliably expected to exhibit similar efficacy in the contemplated active control trial. To this end, the new trial should have the same important design features (primary variables, the dose of the active comparator, eligibility criteria, etc.) as the previously conducted superiority trials in which the active comparator clearly demonstrated clinically relevant efficacy, taking into account advances in medical or statistical practice relevant to the new trial. It is vital that the protocol of a trial designed to demonstrate equivalence or noninferiority contain a clear statement that this is its explicit intention. An equivalence margin should be specified in the protocol; this margin is the largest difference that can be judged as being clinically acceptable and should be smaller than differences observed in superiority trials of the active comparator. For the active control equivalence trial, both the upper and the lower equivalence margins are needed, while only the lower margin is needed for the active control non-inferiority trial. The choice of equivalence margins should be justified clinically. Statistical analysis is generally based on the use of confidence intervals (see Section 5.5). For equivalence trials, two-sided confidence intervals should be used. Equivalence is inferred when the entire confidence interval falls within the equivalence margins. Operationally, this is equivalent to the method of using two simultaneous one-sided tests to test the (composite) null hypothesis that the treatment difference is outside the equivalence margins versus the (composite) alternative hypothesis that the treatment difference is within the margins. Because the two null hypotheses are disjoint, the type I error is appropriately controlled. For 15 Statistical Principles for Clinical Trials non-inferiority trials a one-sided interval should be used. The confidence interval approach has a one-sided hypothesis test counterpart for testing the null hypothesis that the treatment difference (investigational product minus control) is equal to the lower equivalence margin versus the alternative that the treatment difference is greater than the lower equivalence margin. The choice of type I error should be a consideration separate from the use of a one-sided or two-sided procedure. Sample size calculations should be based on these methods (see Section 3.5). Concluding equivalence or non-inferiority based on observing a non-significant test result of the null hypothesis that there is no difference between the investigational product and the active comparator is inappropriate. There are also special issues in the choice of analysis sets. Subjects who withdraw or dropout of the treatment group or the comparator group will tend to have a lack of response, and hence the results of using the full analysis set (see Glossary) may be biased toward demonstrating equivalence (see Section 5.2.3). 3.3.3 Trials to Show Dose-response Relationship How response is related to the dose of a new investigational product is a question to which answers may be obtained in all phases of development, and by a variety of approaches (see ICH E4). Dose-response trials may serve a number of objectives, amongst which the following are of particular importance: the confirmation of efficacy; the investigation of the shape and location of the dose-response curve; the estimation of an appropriate starting dose; the identification of optimal strategies for individual dose adjustments; the determination of a maximal dose beyond which additional benefit would be unlikely to occur. These objectives should be addressed using the data collected at a number of doses under investigation, including a placebo (zero dose) wherever appropriate. For this purpose the application of procedures to estimate the relationship between dose and response, including the construction of confidence intervals and the use of graphical methods, is as important as the use of statistical tests. The hypothesis tests that are used may need to be tailored to the natural ordering of doses or to particular questions regarding the shape of the dose-response curve (e.g. monotonicity). The details of the planned statistical procedures should be given in the protocol. 3.4 Group Sequential Designs Group sequential designs are used to facilitate the conduct of interim analysis (see section 4.5 and Glossary). While group sequential designs are not the only acceptable types of designs permitting interim analysis, they are the most commonly applied because it is more practicable to assess grouped subject outcomes at periodic intervals during the trial than on a continuous basis as data from each subject become available. The statistical methods should be fully specified in advance of the availability of information on treatment outcomes and subject treatment assignments (i.e. blind breaking, see Section 4.5). An Independent Data Monitoring Committee (see Glossary) may be used to review or to conduct the interim analysis of data arising from a group sequential design (see Section 4.6). While the design has been most widely and successfully used in large, long-term trials of mortality or major non-fatal endpoints, its use is growing in other circumstances. In particular, it is recognised that safety must be monitored in all trials and therefore the need for formal procedures to cover early stopping for safety reasons should always be considered. 3.5 Sample Size The number of subjects in a clinical trial should always be large enough to provide a reliable answer to the questions addressed. This number is usually determined by the 16 Statistical Principles for Clinical Trials primary objective of the trial. If the sample size is determined on some other basis, then this should be made clear and justified. For example, a trial sized on the basis of safety questions or requirements or important secondary objectives may need larger numbers of subjects than a trial sized on the basis of the primary efficacy question (see, for example, ICH E1a). Using the usual method for determining the appropriate sample size, the following items should be specified: a primary variable, the test statistic, the null hypothesis, the alternative ('working') hypothesis at the chosen dose(s) (embodying consideration of the treatment difference to be detected or rejected at the dose and in the subject population selected), the probability of erroneously rejecting the null hypothesis (the type I error), and the probability of erroneously failing to reject the null hypothesis (the type II error), as well as the approach to dealing with treatment withdrawals and protocol violations. In some instances, the event rate is of primary interest for evaluating power, and assumptions should be made to extrapolate from the required number of events to the eventual sample size for the trial. The method by which the sample size is calculated should be given in the protocol, together with the estimates of any quantities used in the calculations (such as variances, mean values, response rates, event rates, difference to be detected). The basis of these estimates should also be given. It is important to investigate the sensitivity of the sample size estimate to a variety of deviations from these assumptions and this may be facilitated by providing a range of sample sizes appropriate for a reasonable range of deviations from assumptions. In confirmatory trials, assumptions should normally be based on published data or on the results of earlier trials. The treatment difference to be detected may be based on a judgement concerning the minimal effect which has clinical relevance in the management of patients or on a judgement concerning the anticipated effect of the new treatment, where this is larger. Conventionally the probability of type I error is set at 5% or less or as dictated by any adjustments made necessary for multiplicity considerations; the precise choice may be influenced by the prior plausibility of the hypothesis under test and the desired impact of the results. The probability of type II error is conventionally set at 10% to 20%; it is in the sponsor’s interest to keep this figure as low as feasible especially in the case of trials that are difficult or impossible to repeat. Alternative values to the conventional levels of type I and type II error may be acceptable or even preferable in some cases. Sample size calculations should refer to the number of subjects required for the primary analysis. If this is the 'full analysis set', estimates of the effect size may need to be reduced compared to the per protocol set (see Glossary). This is to allow for the dilution of the treatment effect arising from the inclusion of data from patients who have withdrawn from treatment or whose compliance is poor. The assumptions about variability may also need to be revised. The sample size of an equivalence trial or a non-inferiority trial (see Section 3.3.2) should normally be based on the objective of obtaining a confidence interval for the treatment difference that shows that the treatments differ at most by a clinically acceptable difference. When the power of an equivalence trial is assessed at a true difference of zero, then the sample size necessary to achieve this power is underestimated if the true difference is not zero. When the power of a non-inferiority trial is assessed at a zero difference, then the sample size needed to achieve that power will be underestimated if the effect of the investigational product is less than that of the active control. The choice of a 'clinically acceptable’ difference needs justification with respect to its meaning for future patients, and may be smaller than the 'clinically relevant' difference referred to above in the context of superiority trials designed to establish that a difference exists. 17 Statistical Principles for Clinical Trials The exact sample size in a group sequential trial cannot be fixed in advance because it depends upon the play of chance in combination with the chosen stopping guideline and the true treatment difference. The design of the stopping guideline should take into account the consequent distribution of the sample size, usually embodied in the expected and maximum sample sizes. When event rates are lower than anticipated or variability is larger than expected, methods for sample size re-estimation are available without unblinding data or making treatment comparisons (see Section 4.4). 3.6 Data Capture and Pr ocessing The collection of data and transfer of data from the investigator to the sponsor can take place through a variety of media, including paper case record forms, remote site monitoring systems, medical computer systems and electronic transfer. Whatever data capture instrument is used, the form and content of the information collected should be in full accordance with the protocol and should be established in advance of the conduct of the clinical trial. It should focus on the data necessary to implement the planned analysis, including the context information (such as timing assessments relative to dosing) necessary to confirm protocol compliance or identify important protocol deviations. ‘Missing values’ should be distinguishable from the ‘value zero’ or ‘characteristic absent’. The process of data capture through to database finalisation should be carried out in accordance with GCP (see ICH E6, Section 5). Specifically, timely and reliable processes for recording data and rectifying errors and omissions are necessary to ensure delivery of a quality database and the achievement of the trial objectives through the implementation of the planned analysis. IV. TRIAL CONDUCT CONSIDERATIONS 4.1 Trial Monitoring and Interim Analysis Careful conduct of a clinical trial according to the protocol has a major impact on the credibility of the results (see ICH E6). Careful monitoring can ensure that difficulties are noticed early and their occurrence or recurrence minimised. There are two distinct types of monitoring that generally characterise confirmatory clinical trials sponsored by the pharmaceutical industry. One type of monitoring concerns the oversight of the quality of the trial, while the other type involves breaking the blind to make treatment comparisons (i.e. interim analysis). Both types of trial monitoring, in addition to entailing different staff responsibilities, involve access to different types of trial data and information, and thus different principles apply for the control of potential statistical and operational bias. For the purpose of overseeing the quality of the trial the checks involved in trial monitoring may include whether the protocol is being followed, the acceptability of data being accrued, the success of planned accrual targets, the appropriateness of the design assumptions, success in keeping patients in the trials, etc. (see Sections 4.2 to 4.4). This type of monitoring does not require access to information on comparative treatment effects, nor unblinding of data and therefore has no impact on type I error. The monitoring of a trial for this purpose is the responsibility of the sponsor (see ICH E6) and can be carried out by the sponsor or an independent group selected by the sponsor. The period for this type of monitoring usually starts with the selection of the trial sites and ends with the collection and cleaning of the last subject’s data. The other type of trial monitoring (interim analysis) involves the accruing of comparative treatment results. Interim analysis requires unblinded (i.e. key 18 Statistical Principles for Clinical Trials breaking) access to treatment group assignment (actual treatment assignment or identification of group assignment) and comparative treatment group summary information. This necessitates that the protocol (or appropriate amendments prior to a first analysis) contains statistical plans for the interim analysis to prevent certain types of bias. This is discussed in Sections 4.5 & 4.6. 4.2 Changes in Inclusion and Exclusion Criteria Inclusion and exclusion criteria should remain constant, as specified in the protocol, throughout the period of subject recruitment. Changes may occasionally be appropriate, for example, in long term trials, where growing medical knowledge either from outside the trial or from interim analyses may suggest a change of entry criteria. Changes may also result from the discovery by monitoring staff that regular violations of the entry criteria are occurring, or that seriously low recruitment rates are due to over-restrictive criteria. Changes should be made without breaking the blind and should always be described by a protocol amendment which should cover any statistical consequences, such as sample size adjustments arising from different event rates, or modifications to the planned analysis, such as stratifying the analysis according to modified inclusion/exclusion criteria. 4.3 Accrual Rates In trials with a long time-scale for the accrual of subjects, the rate of accrual should be monitored and, if it falls appreciably below the projected level, the reasons should be identified and remedial actions taken in order to protect the power of the trial and alleviate concerns about selective entry and other aspects of quality. In a multicentre trial these considerations apply to the individual centres. 4.4 Sample Size Adjustment In long term trials there will usually be an opportunity to check the assumptions which underlay the original design and sample size calculations. This may be particularly important if the trial specifications have been made on preliminary and/or uncertain information. An interim 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 be calculated using suitably modified assumptions, and should be justified and documented in a protocol amendment and in the clinical study report. The steps taken to preserve blindness and the consequences, if any, for the type I error and the width of confidence intervals should be explained. The potential need for re-estimation of the sample size should be envisaged in the protocol whenever possible (see Section 3.5). 4.5 Interim Analysis and Early Stopping An interim analysis is any analysis intended to compare treatment arms with respect to efficacy or safety at any time prior to formal completion of a trial. Because the number, methods and consequences of these comparisons affect the interpretation of the trial, all interim analyses should be carefully planned in advance and described in the protocol. Special circumstances may dictate the need for an interim analysis that was not defined at the start of a trial. In these cases, a protocol amendment describing the interim analysis should be completed prior to unblinded access to treatment comparison data. When an interim analysis is planned with the intention of deciding whether or not to terminate a trial, this is usually accomplished by the use of a group sequential design which employs statistical monitoring schemes as guidelines (see Section 3.4). The goal of such an interim analysis is to stop the trial early if the superiority of the treatment under study is clearly established, if the 19 Statistical Principles for Clinical Trials demonstration of a relevant treatment difference has become unlikely or if unacceptable adverse effects are apparent. Generally, boundaries for monitoring efficacy require more evidence to terminate a trial early (i.e. they are more conservative) than boundaries for monitoring safety. When the trial design and monitoring objective involve multiple endpoints then this aspect of multiplicity may also need to be taken into account. The protocol should describe the schedule of interim analyses, or at least the considerations which will govern its generation, for example if flexible alpha spending function approaches are to be employed; further details may be given in a protocol amendment before the time of the first interim analysis. The stopping guidelines and their properties should be clearly described in the protocol or amendments. The potential effects of early stopping on the analysis of other important variables should also be considered. This material should be written or approved by the Data Monitoring Committee (see Section 4.6), when the trial has one. Deviations from the planned procedure always bear the potential of invalidating the trial results. If it becomes necessary to make changes to the trial, any consequent changes to the statistical procedures should be specified in an amendment to the protocol at the earliest opportunity, especially discussing the impact on any analysis and inferences that such changes may cause. The procedures selected should always ensure that the overall probability of type I error is controlled. The execution of an interim analysis should be a completely confidential process because unblinded data and results are potentially involved. All staff involved in the conduct of the trial should remain blind to the results of such analyses, because of the possibility that their attitudes to the trial will be modified and cause changes in the characteristics of patients to be recruited or biases in treatment comparisons. This principle may be applied to all investigator staff and to staff employed by the sponsor except for those who are directly involved in the execution of the interim analysis. Investigators should only be informed about the decision to continue or to discontinue the trial, or to implement modifications to trial procedures. Most clinical trials intended to support the efficacy and safety of an investigational product should proceed to full completion of planned sample size accrual; trials should be stopped early only for ethical reasons or if the power is no longer acceptable. However, it is recognised that drug development plans involve the need for sponsor access to comparative treatment data for a variety of reasons, such as planning other trials. It is also recognised that only a subset of trials will involve the study of serious life-threatening outcomes or mortality which may need sequential monitoring of accruing comparative treatment effects for ethical reasons. In either of these situations, plans for interim statistical analysis should be in place in the protocol or in protocol amendments prior to the unblinded access to comparative treatment data in order to deal with the potential statistical and operational bias that may be introduced. For many clinical trials of investigational products, especially those that have major public health significance, the responsibility for monitoring comparisons of efficacy and/or safety outcomes should be assigned to an external independent group, often called an Independent Data Monitoring Committee (IDMC), a Data and Safety Monitoring Board or a Data Monitoring Committee whose responsibilities should be clearly described. When a sponsor assumes the role of monitoring efficacy or safety comparisons and therefore has access to unblinded comparative information, particular care should be taken to protect the integrity of the trial and to manage and limit appropriately the sharing of information. The sponsor should assure and document that the internal 20 Statistical Principles for Clinical Trials monitoring committee has complied with written standard operating procedures and that minutes of decision making meetings including records of interim results are maintained. Any interim analysis that is not planned appropriately (with or without the consequences of stopping the trial early) may flaw the results of a trial and possibly weaken confidence in the conclusions drawn. Therefore, such analyses should be avoided. If unplanned interim analysis is conducted, the clinical study report should explain why it was necessary, the degree to which blindness had to be broken, provide an assessment of the potential magnitude of bias introduced, and the impact on the interpretation of the results. 4.6 Role of Independent Data Monitoring Committee (IDMC) (see Sections 1.25 and 5.52 of ICH E6) An IDMC may be established by the sponsor to assess at intervals the progress of a clinical trial, safety data, and critical efficacy variables and recommend to the sponsor whether to continue, modify or terminate a trial. The IDMC should have written operating procedures and maintain records of all its meetings, including interim results; these should be available for review when the trial is complete. The independence of the IDMC is intended to control the sharing of important comparative information and to protect the integrity of the clinical trial from adverse impact resulting from access to trial information. The IDMC is a separate entity from an Institutional Review Board (IRB) or an Independent Ethics Committee (IEC), and its composition should include clinical trial scientists knowledgeable in the appropriate disciplines including statistics. When there are sponsor representatives on the IDMC, their role should be clearly defined in the operating procedures of the committee (for example, covering whether or not they can vote on key issues). Since these sponsor staff would have access to unblinded information, the procedures should also address the control of dissemination of interim trial results within the sponsor organisation. V. DATA ANALYSIS CONSIDERATIONS 5.1 Prespecification of the Analysis When designing a clinical trial the principal features of the eventual statistical analysis of the data should be described in the statistical section of the protocol. This section should include all the principal features of the proposed confirmatory analysis of the primary variable(s) and the way in which anticipated analysis problems will be handled. In case of exploratory trials this section could describe more general principles and directions. The statistical analysis plan (see Glossary) may be written as a separate document to be completed after finalising the protocol. In this document, a more technical and detailed elaboration of the principal features stated in the protocol may be included (see section 7.1). The plan may include detailed procedures for executing the statistical analysis of the primary and secondary variables and other data. The plan should be reviewed and possibly updated as a result of the blind review of the data (see 7.1 for definition) and should be finalised before breaking the blind. Formal records should be kept of when the statistical analysis plan was finalised as well as when the blind was subsequently broken. If the blind review suggests changes to the principal features stated in the protocol, these should be documented in a protocol amendment. Otherwise, it will suffice to update the statistical analysis plan with the considerations suggested from the blind 21 Statistical Principles for Clinical Trials review. Only results from analyses envisaged in the protocol (including amendments) can be regarded as confirmatory. In the statistical section of the clinical study report the statistical methodology should be clearly described including when in the clinical trial process methodology decisions were made (see ICH E3). 5.2 Analysis Sets The set of subjects whose data are to be included in the main analyses should be defined in the statistical section of the protocol. In addition, documentation for all subjects for whom trial procedures (e.g. run-in period) were initiated may be useful. The content of this subject documentation depends on detailed features of the particular trial, but at least demographic and baseline data on disease status should be collected whenever possible. If all subjects randomised into a clinical trial satisfied all entry criteria, followed all trial procedures perfectly with no losses to follow-up, and provided complete data records, then the set of subjects to be included in the analysis would be self-evident. The design and conduct of a trial should aim to approach this ideal as closely as possible, but, in practice, it is doubtful if it can ever be fully achieved. Hence, the statistical section of the protocol should address anticipated problems prospectively in terms of how these affect the subjects and data to be analysed. The protocol should also specify procedures aimed at minimising any anticipated irregularities in study conduct that might impair a satisfactory analysis, including various types of protocol violations, withdrawals and missing values. The protocol should consider ways both to reduce the frequency of such problems, and also to handle the problems that do occur in the analysis of data. Possible amendments to the way in which the analysis will deal with protocol violations should be identified during the blind review. It is desirable to identify any important protocol violation with respect to the time when it occurred, its cause and influence on the trial result. The frequency and type of protocol violations, missing values, and other problems should be documented in the clinical study report and their potential influence on the trial results should be described (see ICH E3). Decisions concerning the analysis set should be guided by the following principles : 1) to minimise bias, and 2) to avoid inflation of type I error. 5.2.1 Full Analysis Set The intention-to-treat (see Glossary) principle implies that the primary analysis should include all randomised subjects. Compliance with this principle would necessitate complete follow-up of all randomised subjects for study outcomes. In practice this ideal may be difficult to achieve, for reasons to be described. In this document the term 'full analysis set' is used to describe the analysis set which is as complete as possible and as close as possible to the intention-to-treat ideal of including all randomised subjects. Preservation of the initial randomisation in analysis is important in preventing bias and in providing a secure foundation for statistical tests. In many clinical trials the use of the full analysis set provides a conservative strategy. Under many circumstances it may also provide estimates of treatment effects which are more likely to mirror those observed in subsequent practice. There are a limited number of circumstances that might lead to excluding randomised subjects from the full analysis set including the failure to satisfy major entry criteria (eligibility violations), the failure to take at least one dose of trial medication and the lack of any data post randomisation. Such exclusions should always be justified. 22 Statistical Principles for Clinical Trials Subjects who fail to satisfy an entry criterion may be excluded from the analysis without the possibility of introducing bias only under the following circumstances: (i) the entry criterion was measured prior to randomisation; (ii) the detection of the relevant eligibility violations can be made completely objectively; (iii) all subjects receive equal scrutiny for eligibility violations; (This may be difficult to ensure in an open-label study, or even in a double-blind study if the data are unblinded prior to this scrutiny, emphasising the importance of the blind review.) (iv) all detected violations of the particular entry criterion are excluded. In some situations, it may be reasonable to eliminate from the set of all randomised subjects any subject who took no trial medication. The intention-to-treat principle would be preserved despite the exclusion of these patients provided, for example, that the decision of whether or not to begin treatment could not be influenced by knowledge of the assigned treatment. In other situations it may be necessary to eliminate from the set of all randomised subjects any subject without data post randomisation. No analysis is complete unless the potential biases arising from these specific exclusions, or any others, are addressed. When the full analysis set of subjects is used, violations of the protocol that occur after randomisation may have an impact on the data and conclusions, particularly if their occurrence is related to treatment assignment. In most respects it is appropriate to include the data from such subjects in the analysis, consistent with the intentionto-treat principle. Special problems arise in connection with subjects withdrawn from treatment after receiving one or more doses who provide no data after this point, and subjects otherwise lost to follow-up, because failure to include these subjects in the full analysis set may seriously undermine the approach. Measurements of primary variables made at the time of the loss to follow-up of a subject for any reason, or subsequently collected in accordance with the intended schedule of assessments in the protocol, are valuable in this context; subsequent collection is especially important in studies where the primary variable is mortality or serious morbidity. The intention to collect data in this way should be described in the protocol. Imputation techniques, ranging from the carrying forward of the last observation to the use of complex mathematical models, may also be used in an attempt to compensate for missing data. Other methods employed to ensure the availability of measurements of primary variables for every subject in the full analysis set may require some assumptions about the subjects' outcomes or a simpler choice of outcome (e.g. success / failure). The use of any of these strategies should be described and justified in the statistical section of the protocol and the assumptions underlying any mathematical models employed should be clearly explained. It is also important to demonstrate the robustness of the corresponding results of analysis especially when the strategy in question could itself lead to biased estimates of treatment effects. Because of the unpredictability of some problems, it may sometimes be preferable to defer detailed consideration of the manner of dealing with irregularities until the blind review of the data at the end of the trial, and, if so, this should be stated in the protocol. 5.2.2 Per Protocol Set The 'per protocol' set of subjects, sometimes described as the 'valid cases', the 'efficacy' sample or the 'evaluable subjects' sample, defines a subset of the subjects in the full 23 Statistical Principles for Clinical Trials analysis set who are more compliant with the protocol and is characterised by criteria such as the following: (i) the completion of a certain pre-specified minimal exposure to the treatment regimen; (ii) the availability of measurements of the primary variable(s); (iii) the absence of any major protocol violations including the violation of entry criteria. The precise reasons for excluding subjects from the per protocol set should be fully defined and documented before breaking the blind in a manner appropriate to the circumstances of the specific trial. The use of the per protocol set may maximise the opportunity for a new treatment to show additional efficacy in the analysis, and most closely reflects the scientific model underlying the protocol. However, the corresponding test of the hypothesis and estimate of the treatment effect may or may not be conservative depending on the trial; the bias, which may be severe, arises from the fact that adherence to the study protocol may be related to treatment and outcome. The problems that lead to the exclusion of subjects to create the per protocol set, and other protocol violations, should be fully identified and summarised. Relevant protocol violations may include errors in treatment assignment, the use of excluded medication, poor compliance, loss to follow-up and missing data. It is good practice to assess the pattern of such problems among the treatment groups with respect to frequency and time to occurrence. 5.2.3 Roles of the Different Analysis Sets In general, it is advantageous to demonstrate a lack of sensitivity of the principal trial results to alternative choices of the set of subjects analysed. In confirmatory trials it is usually appropriate to plan to conduct both an analysis of the full analysis set and a per protocol analysis, so that any differences between them can be the subject of explicit discussion and interpretation. In some cases, it may be desirable to plan further exploration of the sensitivity of conclusions to the choice of the set of subjects analysed. When the full analysis set and the per protocol set lead to essentially the same conclusions, confidence in the trial results is increased, bearing in mind, however, that the need to exclude a substantial proportion of subjects from the per protocol analysis throws some doubt on the overall validity of the trial. The full analysis set and the per protocol set play different roles in superiority trials (which seek to show the investigational product to be superior), and in equivalence or non-inferiority trials (which seek to show the investigational product to be comparable, see section 3.3.2). In superiority trials the full analysis set is used in the primary analysis (apart from exceptional circumstances) because it tends to avoid over-optimistic estimates of efficacy resulting from a per protocol analysis, since the non-compliers included in the full analysis set will generally diminish the estimated treatment effect. However, in an equivalence or non-inferiority trial use of the full analysis set is generally not conservative and its role should be considered very carefully. 5.3 Missing Values and Outliers Missing values represent a potential source of bias in a clinical trial. Hence, every effort should be undertaken to fulfil all the requirements of the protocol concerning the collection and management of data. In reality, however, there will almost always 24 Statistical Principles for Clinical Trials be some missing data. A trial may be regarded as valid, nonetheless, provided the methods of dealing with missing values are sensible, and particularly if those methods are pre-defined in the protocol. Definition of methods may be refined by updating this aspect in the statistical analysis plan during the blind review. Unfortunately, no universally applicable methods of handling missing values can be recommended. An investigation should be made concerning the sensitivity of the results of analysis to the method of handling missing values, especially if the number of missing values is substantial. A similar approach should be adopted to exploring the influence of outliers, the statistical definition of which is, to some extent, arbitrary. Clear identification of a particular value as an outlier is most convincing when justified medically as well as statistically, and the medical context will then often define the appropriate action. Any outlier procedure set out in the protocol or the statistical analysis plan should be such as not to favour any treatment group a priori. Once again, this aspect of the analysis can be usefully updated during blind review. If no procedure for dealing with outliers was foreseen in the trial protocol, one analysis with the actual values and at least one other analysis eliminating or reducing the outlier effect should be performed and differences between their results discussed. 5.4 Data Transfor mation The decision to transform key variables prior to analysis is best made during the design of the 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 of transformations to ensure that the assumptions underlying the statistical methods are met are to be found in standard texts; conventions for particular variables have been developed in a number of specific clinical areas. The decision on whether and how to transform a variable should be influenced by the preference for a scale which facilitates clinical interpretation. Similar considerations apply to other derived variables, such as the use of change from baseline, percentage change from baseline, the 'area under the curve' of repeated measures, or the ratio of two different variables. Subsequent clinical interpretation should be carefully considered, and the derivation should be justified in the protocol. Closely related points are made in Section 2.2.2. 25 Statistical Principles for Clinical Trials 5.5 Estimation, Confidence Intervals and Hypothesis Testing The statistical section of the protocol should specify the hypotheses that are to be tested and/or the treatment effects which are to be estimated in order to satisfy the primary objectives of the trial. The statistical 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 be made 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. A description should be given of any intentions to use baseline data to improve precision or to adjust estimates for potential baseline differences, for example by means of analysis of covariance. It is important 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 hypothesis tests are not considered appropriate, then the alternative process for arriving at statistical conclusions should be given. The issue of one-sided or two-sided approaches to inference is controversial and a diversity of views can be found in the statistical literature. The approach of setting type I errors for one-sided tests at half the conventional type I error used in two-sided tests is preferable in regulatory settings. This promotes consistency with the two-sided confidence intervals that are generally appropriate for estimating the possible size of the difference between two treatments. The particular statistical model chosen should reflect the current state of medical and statistical knowledge about the variables to be analysed as well as the statistical design of the trial. All effects to be fitted in the analysis (for example in analysis of variance models) should be fully specified, and the manner, if any, in which this set of effects might be modified in response to preliminary results should be explained. The same considerations apply to the set of covariates fitted in an analysis of covariance. (See also Section 5.7.). In the choice of statistical methods due attention should be paid to the statistical distribution of both primary and secondary variables. When making this choice (for example between parametric and non-parametric methods) it is important to bear in mind the need to provide statistical estimates of the size of treatment effects together with confidence intervals (in addition to significance tests). The primary analysis of the primary variable should be clearly distinguished from supporting analyses of the primary or secondary variables. Within the statistical section of the protocol or the statistical analysis plan there should also be an outline of the way in which data other than the primary and secondary variables will be summarised and reported. This should include a reference to any approaches adopted for the purpose of achieving consistency of analysis across a range of trials, for example for safety data. Modelling approaches that incorporate information on known pharmacological parameters, the extent of protocol compliance for individual subjects or other biologically based data may provide valuable insights into actual or potential efficacy, especially with regard to estimation of treatment effects. The assumptions underlying such models should always be clearly identified, and the limitations of any conclusions should be carefully described. 5.6 Adjustment of Significance and Confidence Levels When multiplicity is present, the usual frequentist approach to the analysis of clinical trial data may necessitate an adjustment to the type I error. Multiplicity may arise, for example, from multiple primary variables (see Section 2.2.2), multiple comparisons of treatments, repeated evaluation over time and/or interim analyses 26 Statistical Principles for Clinical Trials (see Section 4.5). Methods to avoid or reduce multiplicity are sometimes preferable when available, such as the identification of the key primary variable (multiple variables), the choice of a critical treatment contrast (multiple comparisons), the use of a summary measure such as ‘area under the curve’ (repeated measures). In confirmatory analyses, any aspects of multiplicity which remain after steps of this kind have been taken should be identified in the protocol; adjustment should always be considered and the details of any adjustment procedure or an explanation of why adjustment is not thought to be necessary should be set out in the analysis plan. 5.7 Subgroups, Interactions and Covariates The primary variable(s) is often systematically related to other influences apart from treatment. For example, there may be relationships to covariates such as age and sex, or there may be differences between specific subgroups of subjects such as those treated at the different centres of a multicentre trial. In some instances an adjustment for the influence of covariates or for subgroup effects is an integral part of the planned analysis and hence should be set out in the protocol. Pre-trial deliberations should identify those covariates and factors expected to have an important influence on the primary variable(s), and should consider how to account for these in the analysis in order to improve precision and to compensate for any lack of balance between treatment groups. If one or more factors are used to stratify the design, it is appropriate to account for those factors in the analysis. When the potential value of an adjustment is in doubt, it is often advisable to nominate the unadjusted analysis as the one for primary attention, the adjusted analysis being supportive. Special attention should be paid to centre effects and to the role of baseline measurements of the primary variable. It is not advisable to adjust the main analyses for covariates measured after randomisation because they may be affected by the treatments. The treatment effect itself may also vary with subgroup or covariate - for example, the effect may decrease with age or may be larger in a particular diagnostic category of subjects. In some cases such interactions are anticipated or are of particular prior interest (e.g. geriatrics), and hence a subgroup analysis, or a statistical model including interactions, is part of the planned confirmatory analysis. In most cases, however, subgroup or interaction analyses are exploratory and should be clearly identified as such; they should explore the uniformity of any treatment effects found overall. In general, such analyses should proceed first through the addition of interaction terms to the statistical model in question, complemented by additional exploratory analysis within relevant subgroups of subjects, or within strata defined by the covariates. When exploratory, these analyses should be interpreted cautiously; any conclusion of treatment efficacy (or lack thereof) or safety based solely on exploratory subgroup analyses are unlikely to be accepted. 5.8 Integrity of Data and Com puter Software Validity The credibility of the numerical results of the analysis depends on the quality and validity of the methods and software (both internally and externally written) used both for data management (data entry, storage, verification, correction and retrieval) and also for processing the data statistically. Data management activities should therefore be based on thorough and effective standard operating procedures. The computer software used for data management and statistical analysis should be reliable, and documentation of appropriate software testing procedures should be available. 27 Statistical Principles for Clinical Trials VI. EVALUATION OF SAFETY AND TOLERABILITY 6.1 Scope of Evaluation In all clinical trials evaluation of safety and tolerability (see Glossary) constitutes an important element. In early phases this evaluation is mostly of an exploratory nature, and is only sensitive to frank expressions of toxicity, whereas in later phases the establishment of the safety and tolerability profile of a drug can be characterised more fully in larger samples of subjects. Later phase controlled trials represent an important means of exploring in an unbiased manner any new potential adverse effects, even if such trials generally lack power in this respect. Certain trials may be designed with the purpose of making specific claims about superiority or equivalence with regard to safety and tolerability compared to another drug or to another dose of the investigational drug. Such specific claims should be supported by relevant evidence from confirmatory trials, similar to that necessary for corresponding efficacy claims. 6.2 Choice of Variables and Data Collection In any clinical trial the methods and measurements chosen to evaluate the safety and tolerability of a drug will depend on a number of factors, including knowledge of the adverse effects of closely related drugs, information from non-clinical and earlier clinical trials and possible consequences of the pharmacodynamic/pharmacokinetic properties of the particular drug, the mode of administration, the type of subjects to be studied, and the duration of the trial. Laboratory tests concerning clinical chemistry and haematology, vital signs, and clinical adverse events (diseases, signs and symptoms) usually form the main body of the safety and tolerability data. The occurrence of serious adverse events and treatment discontinuations due to adverse events are particularly important to register (see ICH E2A and ICH E3). Furthermore, it is recommended that a consistent methodology be used for the data collection and evaluation throughout a clinical trial program in order to facilitate the combining of data from different trials. The use of a common adverse event dictionary is particularly important. This dictionary has a structure which gives the possibility to summarise the adverse event data on three different levels; system-organ class, preferred term or included term (see Glossary). The preferred term is the level on which adverse events usually are summarised, and preferred terms belonging to the same system-organ class could then be brought together in the descriptive presentation of data (see ICH M1). 6.3 Set of Subjects to be Evaluated and Presentation of Data For the overall safety and tolerability assessment, the set of subjects to be summarised is usually defined as those subjects who received at least one dose of the investigational drug. Safety and tolerability variables should be collected as comprehensively as possible from these subjects, including type of adverse event, severity, onset and duration (see ICH E2B). Additional safety and tolerability evaluations may be needed in specific subpopulations, such as females, the elderly (see ICH E7), the severely ill, or those who have a common concomitant treatment. These evaluations may need to address more specific issues (see ICH E3). All safety and tolerability variables will need attention during evaluation, and the broad approach should be indicated in the protocol. All adverse events should be reported, whether or not they are considered to be related to treatment. All available data in the study population should be accounted for in the evaluation. Definitions of measurement units and reference ranges of laboratory variables should be made with care; if different units or different reference ranges appear in the same trial (e.g. if 28 Statistical Principles for Clinical Trials more than one laboratory is involved), then measurements should be appropriately standardised to allow a unified evaluation. Use of a toxicity grading scale should be prespecified and justified. The incidence of a certain adverse event is usually expressed in the form of a proportion relating number of subjects experiencing events to number of subjects at risk. However, it is not always self-evident how to assess incidence. For example, depending on the situation the number of exposed subjects or the extent of exposure (in person-years) could be considered for the denominator. Whether the purpose of the calculation is to estimate a risk or to make a comparison between treatment groups it is important that the definition is given in the protocol. This is especially important if long-term treatment is planned and a substantial proportion of treatment withdrawals or deaths are expected. For such situations survival analysis methods should be considered and cumulative adverse event rates calculated in order to avoid the risk of underestimation. In situations when there is a substantial background noise of signs and symptoms (e.g. in psychiatric trials) one should consider ways of accounting for this in the estimation of risk for different adverse events. One such method is to make use of the 'treatment emergent' (see Glossary) concept in which adverse events are recorded only if they emerge or worsen relative to pretreatment baseline. Other methods to reduce the effect of the background noise may also be appropriate such as ignoring adverse events of mild severity or requiring that an event should have been observed at repeated visits to qualify for inclusion in the numerator. Such methods should be explained and justified in the protocol. 6.4 Statistical Evaluation The investigation of safety and tolerability is a multidimensional problem. Although some specific adverse effects can usually be anticipated and specifically monitored for any drug, the range of possible adverse effects is very large, and new and unforeseeable effects are always possible. Further, an adverse event experienced after a protocol violation, such as use of an excluded medication, may introduce a bias. This background underlies the statistical difficulties associated with the analytical evaluation of safety and tolerability of drugs, and means that conclusive information from confirmatory clinical trials is the exception rather than the rule. In most trials the safety and tolerability implications are best addressed by applying descriptive statistical methods to the data, supplemented by calculation of confidence intervals wherever this aids interpretation. It is also valuable to make use of graphical presentations in which patterns of adverse events are displayed both within treatment groups and within subjects. The calculation of p-values is sometimes useful either as an aid to evaluating a specific difference of interest, or as a 'flagging' device applied to a large number of safety and tolerability variables to highlight differences worth further attention. This is particularly useful for laboratory data, which otherwise can be difficult to summarise appropriately. It is recommended that laboratory data be subjected to both a quantitative analysis, e.g. evaluation of treatment means, and a qualitative analysis where counting of numbers above or below certain thresholds are calculated. If hypothesis tests are used, statistical adjustments for multiplicity to quantify the type I error are appropriate, but the type II error is usually of more concern. Care should be taken when interpreting putative statistically significant findings when there is no multiplicity adjustment. 29 Statistical Principles for Clinical Trials In the majority of trials investigators are seeking to establish that there are no clinically unacceptable differences in safety and tolerability compared with either a comparator drug or a placebo. As is the case for non-inferiority or equivalence evaluation of efficacy the use of confidence intervals is preferred to hypothesis testing in this situation. In this way, the considerable imprecision often arising from low frequencies of occurrence is clearly demonstrated. 6.5 Integrated Summary The safety and tolerability properties of a drug are commonly summarised across trials continuously during an investigational product’s development and in particular at the time of a marketing application. The usefulness of this summary, however, is dependent on adequate and well-controlled individual trials with high data quality. The overall usefulness of a drug is always a question of balance between risk and benefit and in a single trial such a perspective could also be considered, even if the assessment of risk/benefit usually is performed in the summary of the entire clinical trial program. (See section 7.2.2) For more details on the reporting of safety and tolerability, see Chapter 12 of ICH E3. VII. REPORTING 7.1 Evaluation and Reporting As stated in the Introduction, the structure and content of clinical study reports is the subject of ICH E3. That ICH guidance fully covers the reporting of statistical work, appropriately integrated with clinical and other material. The current section is therefore relatively brief. During the planning phase of a trial the principal features of the analysis should have been specified in the protocol as described in Section 5. When the conduct of the trial is over and the data are assembled and available for preliminary inspection, it is valuable to carry out the blind review of the planned analysis also described in Section 5. This pre-analysis review, blinded to treatment, should cover decisions concerning, for example, the exclusion of subjects or data from the analysis sets; possible transformations may also be checked, and outliers defined; important covariates identified in other recent research may be added to the model; the use of parametric or non-parametric methods may be reconsidered. Decisions made at this time should be described in the report, and should be distinguished from those made after the statistician has had access to the treatment codes, as blind decisions will generally introduce less potential for bias. Statisticians or other staff involved in unblinded interim analysis should not participate in the blind review or in making modifications to the statistical analysis plan. When the blinding is compromised by the possibility that treatment induced effects may be apparent in the data, special care will be needed for the blind review. Many of the more detailed aspects of presentation and tabulation should be finalised at or about the time of the blind review so that by the time of the actual analysis full plans exist for all its aspects including subject selection, data selection and modification, data summary and tabulation, estimation and hypothesis testing. 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 the actual analysis as described in the protocol, protocol amendments or the updated statistical analysis plan based on a blind review of data. A careful explanation should be provided for deviations from the planned analysis. 30 Statistical Principles for Clinical Trials All subjects who entered the trial should be accounted for in the report, whether or not they are included in the analysis. All reasons for exclusion from analysis should be documented; for any subject included in the full analysis set but not in the per protocol set, the reasons for exclusion from the latter should also be documented. Similarly, for all subjects included in an analysis set, the measurements of all important variables should be accounted for at all relevant time-points. The effect of all losses of subjects or data, withdrawals from treatment and major protocol violations on the main analyses of the primary variable(s) should be considered carefully. Subjects lost to follow up, withdrawn from treatment, or with a severe protocol violation should be identified, and a descriptive analysis of them provided, including the reasons for their loss and its relationship to treatment and outcome. Descriptive statistics form an indispensable part of reports. Suitable tables and/or graphical presentations should illustrate clearly the important features of the primary and secondary variables and of key prognostic and demographic variables. The results of the main analyses relating to the objectives of the trial should be the subject of particularly careful descriptive presentation. When reporting the results of significance tests, precise p-values (e.g.'p=0.034') should be reported rather than making exclusive reference to critical values. Although the primary goal of the analysis of a clinical trial should be to answer the questions posed by its main objectives, new questions based on the observed data may well emerge during the unblinded analysis. Additional and perhaps complex statistical analysis may be the consequence. This additional work should be strictly distinguished in the report from work which was planned in the protocol. The play of chance may lead to unforeseen imbalances between the treatment groups in terms of baseline measurements not pre-defined as covariates in the planned analysis but having some prognostic importance nevertheless. This is best dealt with by showing that an additional analysis which accounts for these imbalances reaches essentially the same conclusions as the planned analysis. If this is not the case, the effect of the imbalances on the conclusions should be discussed. In general, sparing use should be made of unplanned analyses. Such analyses are often carried out when it is thought that the treatment effect may vary according to some other factor or factors. An attempt may then be made to identify subgroups of subjects for whom the effect is particularly beneficial. The potential dangers of overinterpretation of unplanned subgroup analyses are well known (see also Section 5.7), and should be carefully avoided. Although similar problems of interpretation arise if a treatment appears to have no benefit, or an adverse effect, in a subgroup of subjects, such possibilities should be properly assessed and should therefore be reported. Finally statistical judgement should be brought to bear on the analysis, interpretation and presentation of the results of a clinical trial. To this end the trial statistician should be a member of the team responsible for the clinical study report, and should approve the clinical report. 7.2 Summarising the Clinical Database An overall summary and synthesis of the evidence on safety and efficacy from all the reported clinical trials is required for a marketing application (Expert report in EU, integrated summary reports in USA, Gaiyo in Japan). This may be accompanied, when appropriate, by a statistical combination of results. Within the summary a number of areas of specific statistical interest arise: describing the demography and clinical features of the population treated during the course of 31 Statistical Principles for Clinical Trials the clinical trial programme; addressing the key questions of efficacy by considering the results of the relevant (usually controlled) trials and highlighting the degree to which they reinforce or contradict each other; summarising the safety information available from the combined database of all the trials whose results contribute to the marketing application and identifying potential safety issues. During the design of a clinical programme careful attention should be paid to the uniform definition and collection of measurements which will facilitate subsequent interpretation of the series of trials, particularly if they are likely to be combined across trials. A common dictionary for recording the details of medication, medical history and adverse events should be selected and used. A common definition of the primary and secondary variables is nearly always worthwhile, and essential for meta-analysis. The manner of measuring key efficacy variables, the timing of assessments relative to randomisation/entry, the handling of protocol violators and deviators and perhaps the definition of prognostic factors, should all be kept compatible unless there are valid reasons not to do so. Any statistical procedures used to combine data across trials should be described in detail. Attention should be paid to the possibility of bias associated with the selection of trials, to the homogeneity 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. 7.2.1 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 clinical trials which address essentially identical key efficacy questions. The main results of such a set of trials should be presented in an identical form to permit comparison, usually in 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 a more precise overall estimate of the size of the treatment effects to be generated, and provides a complete and concise summary of the results of the trials. Under exceptional circumstances a meta analytic approach may also be the most appropriate way, or the only way, of providing sufficient overall evidence of efficacy via an overall hypothesis test. When used for this purpose the meta-analysis should have its own prospectively written protocol. 7.2.2 Safety Data In summarising safety data it is important to examine the safety database thoroughly for any indications of potential toxicity, and to follow up any indications by looking for an associated supportive pattern of observations. The combination of the safety data from all human exposure to the drug provides an important source of information, because its larger sample size provides the best chance of detecting the rarer adverse events and, perhaps, of estimating their approximate incidence. However, incidence data from this database are difficult to evaluate because of the lack of a comparator group, and data from comparative trials are especially valuable in overcoming this difficulty. The results from trials which use a common comparator (placebo or specific active comparator) should be combined and presented separately for each comparator providing sufficient data. All indications of potential toxicity arising from exploration of the data should be reported. The evaluation of the reality of these potential adverse effects should take account of the issue of multiplicity arising from the numerous comparisons made. The evaluation should also make appropriate use of survival analysis methods to exploit the potential relationship of the incidence of adverse events to duration of exposure 32 Statistical Principles for Clinical Trials and/or follow-up. The risks associated with identified adverse effects should be appropriately quantified to allow a proper assessment of the risk/benefit relationship. GLOSSARY Bayesian Approaches Approaches to data analysis that provide a posterior probability distribution for some parameter (e.g. treatment effect), derived from the observed data and a prior probability distribution for the parameter. The posterior distribution is then used as the basis for statistical inference. Bias (Statistical & Operational) The systematic tendency of any factors associated with the design, conduct, analysis and evaluation of the results of a clinical trial to make the estimate of a treatment effect deviate from its true value. Bias introduced through deviations in conduct is referred to as 'operational' bias. The other sources of bias listed above are referred to as 'statistical'. Blind Review The checking and assessment of data during the period of time between trial completion (the last observation on the last subject) and the breaking of the blind, for the purpose of finalising the planned analysis. Content Validity The extent to which a variable (e.g. a rating scale) measures what it is supposed to measure. Double-Dummy A technique for retaining the blind when administering supplies in a clinical trial, when the two treatments cannot be made identical. Supplies are prepared for Treatment A (active and indistinguishable placebo) and for Treatment B (active and indistinguishable placebo). Subjects then take two sets of treatment; either A (active) and B (placebo), or A (placebo) and B (active). Dropout A subject in a clinical trial who for any reason fails to continue in the trial until the last visit required of him/her by the study protocol. Equivalence Trial A trial with the primary objective of showing that the response to two or more treatments differs by an amount which is clinically unimportant. This is usually demonstrated by showing that the true treatment difference is likely to lie between a lower and an upper equivalence margin of clinically acceptable differences. Frequentist Methods Statistical methods, such as significance tests and confidence intervals, which can be interpreted in terms of the frequency of certain outcomes occurring in hypothetical repeated realisations of the same experimental situation. Full Analysis Set 33 Statistical Principles for Clinical Trials The set of subjects that is as close as possible to the ideal implied by the intention-totreat principle. It is derived from the set of all randomised subjects by minimal and justified elimination of subjects. Generalisability, Generalisation The extent to which the findings of a clinical trial can be reliably extrapolated from the subjects who participated in the trial to a broader patient population and a broader range of clinical settings. Global Assessment Variable A single variable, usually a scale of ordered categorical ratings, which integrates objective variables and the investigator's overall impression about the state or change in state of a subject. Independent Data Monitoring Committee (IDMC) (Data and Safety Monitoring Board, Monitoring Committee, Data Monitoring Committee) An independent data-monitoring committee that may be established by the sponsor to assess at intervals the progress of a clinical trial, the safety data, and the critical efficacy endpoints, and to recommend to the sponsor whether to continue, modify, or stop a trial. Intention-To-Treat Principle The principle that asserts that the effect of a treatment policy can be best assessed by evaluating on the basis of the intention to treat a subject (i.e. the planned treatment regimen) rather than the actual treatment given. It has the consequence that subjects allocated to a treatment group should be followed up, assessed and analysed as members of that group irrespective of their compliance to the planned course of treatment. Interaction (Qualitative & Quantitative) The situation in which a treatment contrast (e.g. difference between investigational product and control) is dependent on another factor (e.g. centre). A quantitative interaction refers to the case where the magnitude of the contrast differs at the different levels of the factor, whereas for a qualitative interaction the direction of the contrast differs for at least one level of the factor. Inter-Rater Reliability The property of yielding equivalent results when used by different raters on different occasions. Intra-Rater Reliability The property of yielding equivalent results when used by the same rater on different occasions. Interim Analysis Any analysis intended to compare treatment arms with respect to efficacy or safety at any time prior to the formal completion of a trial. Meta-Analysis The formal evaluation of the quantitative evidence from two or more trials bearing on the same question. This most commonly involves the statistical combination of 34 Statistical Principles for Clinical Trials summary statistics from the various trials, but the term is sometimes also used to refer to the combination of the raw data. Multicentre Trial A clinical trial conducted according to a single protocol but at more than one site, and therefore, carried out by more than one investigator. Non-Inferiority Trial A trial with the primary objective of showing that the response to the investigational product is not clinically inferior to a comparative agent (active or placebo control). Preferred and Included Terms In a hierarchical medical dictionary, for example MedDRA, the included term is the lowest level of dictionary term to which the investigator description is coded. The preferred term is the level of grouping of included terms typically used in reporting frequency of occurrence. For example, the investigator text “Pain in the left arm” might be coded to the included term “Joint pain”, which is reported at the preferred term level as “Arthralgia”. Per Protocol Set (Valid Cases, Efficacy Sample, Evaluable Subjects Sample) The set of data generated by the subset of subjects who complied with the protocol sufficiently to ensure that these data would be likely to exhibit the effects of treatment, according to the underlying scientific model. Compliance covers such considerations as exposure to treatment, availability of measurements and absence of major protocol violations. Safety & Tolerability The safety of a medical product concerns the medical risk to the subject, usually assessed in a clinical trial by laboratory tests (including clinical chemistry and haematology), vital signs, clinical adverse events (diseases, signs and symptoms), and other special safety tests (e.g. ECGs, ophthalmology). The tolerability of the medical product represents the degree to which overt adverse effects can be tolerated by the subject. Statistical Analysis Plan A statistical analysis plan is a document that contains a more technical and detailed elaboration of the principal features of the analysis described in the protocol, and includes detailed procedures for executing the statistical analysis of the primary and secondary variables and other data. Superiority Trial A trial with the primary objective of showing that the response to the investigational product is superior to a comparative agent (active or placebo control). Surrogate Variable A variable that provides an indirect measurement of effect in situations where direct measurement of clinical effect is not feasible or practical. Treatment Effect An effect attributed to a treatment in a clinical trial. In most clinical trials the treatment effect of interest is a comparison (or contrast) of two or more treatments. 35 Statistical Principles for Clinical Trials Treatment Emergent An event that emerges during treatment having been absent pre-treatment, or worsens relative to the pre-treatment state. Trial Statistician A statistician who has a combination of education/training and experience sufficient to implement the principles in this guidance and who is responsible for the statistical aspects of the trial. 36 Ruolo di differenti insiemi di pazienti nell’analisi delle sperimentazioni cliniche dr.ssa Bacchieri “Ruolo di differenti insiemi di pazienti nell’analisi delle sperimentazioni cliniche” Antonella Bacchieri Le competenze biostatistiche nell’ambito dei Comitati Etici locali (Roma, 18 marzo 2003) Differenti insiemi di pazienti (Popolazioni) • • • • Safety Full Set ~ Intention-To-Treat (ITT) Completers ( <=> diverse definizioni) Completers/Compliers~Per Protocol~Efficacy Sample~Valid Cases~Evaluable Subjects ( <=> diverse definizioni) • Sotto-gruppi definiti sulla base di uno o più fattori prognostici di interesse Safety~”Full Set” • Definizione: Tutti i pazienti randomizzati, che hanno preso almeno una dose del trattamento in studio • Ruolo: risponde alla domanda: – qual è la sicurezza del trattamento (assunto in qualunque condizione e per qualunque ragione)? Safety~”Full Set”: debolezze • I pazienti drop-out (cioè che interrompono prematuramente lo studio) non hanno una valutazione finale (per esempio per dati di laboratorio e segni vitali) ITT~ ”Full Set” • Definizione rigorosa: Tutti i pazienti randomizzati • Definizione modificata: Tutti i pazienti randomizzati, che hanno preso almeno una dose del trattamento in studio, che hanno almeno una valutazione post-basale (e che soddisfano i criteri di inclusione fondamentali). • Ruolo: risponde alla domanda: – qual è l’effetto del trattamento in condizioni simili a quelle reali? ITT: obiettivi • Fornire una stima dell’effetto del trattamento che sia più vicina possibile alla situazione clinica reale • Lasciare invariate le condizioni create dalla randomizazzione, cioè non introdurre bias di selezione (relativi a fattori prognostici noti o ignoti) e bias di osservazione/valutazione • Permettere di verificare se il pattern dei drop-out è indipendente dal trattamento (verifica indiretta tramite confronto risultati verso Completers) ITT: debolezze • Non escludere alcun paziente dall’analisi generalmente crea un bias • Tuttavia, la direzione di questo bias è nota se sono impiegati metodi appropriati per sostituire i valori mancanti ITT: debolezze • Difficoltà di scelta del metodo per sostituire le osservazioni mancanti – Retrieved drop-out: valutare a fine studio anche i drop-out [ Knapp MJ et al. JAMA 13; 985-991 (1994)] – Last-Observation-Carried-Forward (LOCF): ciascun paziente è inserito nell’analisi con la sua ultima valutazione – Inputation strategy: • assegnare ai drop-out dei valori ricavati da modelli statistici, tesi a stimare i valori che i pazienti con valori mancanti avrebbero avuto se non fossero usciti prematuramente dallo studio (bibliografia allegata) • assegnare ai drop-out valori pre-definiti a seconda della loro ragione di uscita dallo studio [Gould AL. Biometrics 36; 721-727 (1980)] • assegnare ai drop-out il valore peggiore (eventualmente assegnare il valore migliore a quelli del gruppo di controllo) • Metodo di analisi statistica (la scelta deve tenere in considerazione la scelta sopra descritta) ITT: Scelta del metodo • BIAS • INTERPRETABILITA’ • PROBABILITA’ DELL’ERRORE DI PRIMO TIPO • POTENZA Completers (1) • “Completers” relativamente alle visite di valutazione dello studio – Definizione: Tutti i pazienti che hanno una valutazione alla visita finale (o ad un certo numero pre-definito di visite) almeno per l’endpoint primario – Ruolo: “risponde” alla domanda: • qual è l’effetto del trattamento senza influenza delle distorsioni generate dal metodo di sostituzione delle osservazioni mancanti? Completers (2) • “Completers” relativamente all’esposizione al trattamento in studio – Definizione: Tutti i pazienti che hanno avuto un’esposizione completa (o almeno di una certa entità) al trattamento – Ruolo: “risponde” alla domanda: • qual è l’effetto del trattamento nel sotto-insieme dei pazienti che possono/vogliono prendere tutto il trattamento, come definito dal protocollo? Completers: obiettivi • Ottenere stime del trattamento più facilmente interpretabili da un punto di vista clinico rispetto a quelle ottenute sulla popolazione ITT Completers: debolezze • BIAS: i pazienti che completano lo studio possono non essere rappresentativi di tutti i pazienti per ragioni legate al trattamento • Generalmente, interpretabile solo in presenza di un risultato significativo a livello di ITT Completers/Compliers ~Per Protocol ~Efficacy Sample~Valid Cases~Evaluable Subjects (1) • Definizione: Sotto-insieme della popolazione Completers (1) che ha rispettato il protocollo (criteri di eleggibilità, “buona” compliance al trattamento sperimentale, rispetto delle procedure fissate dal protocollo) • Ruolo: “risponde” alla domanda: – qual è l’effetto del trattamento nelle migliori condizioni sperimentali (popolazione target che riesce a completare lo studio come pianificato)? Completers/Compliers ~Per Protocol ~Efficacy Sample~Valid Cases~Evaluable Subjects (2) • Definizione: Sotto-insieme della popolazione ITT che ha rispettato il protocollo (criteri di eleggibilità, “buona” compliance al trattamento sperimentale, rispetto delle procedure fissate dal protocollo) • Ruolo: “risponde” alla domanda: – qual è l’effetto del trattamento nella popolazione target? Completers/Compliers...: obiettivi • Massimizzare le opportunità del trattamento in studio di dimostrare un effetto • Fornire una stima dell’effetto del trattamento che corrisponde al modello scientifico sottostante il protocollo Completers/Compliers...: debolezze • BIAS (potenzialmente rilevante): l’aderenza al protocollo può essere correlata con il trattamento e con il risultato dello studio • Pertanto, interpretabile solo in presenza di un risultato significativo a livello di ITT Sottogruppi definiti sulla base di uno o più fattori prognostici di interesse • Definizione: Sotto-gruppi della popolazione ITT definiti rispetto ai livelli di un fattore prognostico di interesse (es. giovani /anziani, maschi/femmine, ecc…) • Ruolo: le analisi di sotto-gruppo “rispondono” alla domanda: – l’effetto del trattamento varia al variare del fattore prognostico di interesse? (~ C’è interazione trattamento-fattore prognostico?) Sottogruppi definiti sulla base di fattori prognostici: obiettivi • Bisogna distinguere il caso in cui gli strati sono pre-definiti (~definiti da una randomizzazione stratificata) dal caso in cui la stratificazione è introdotta a posteriori • In ogni caso: l’obiettivo principale è quello di generare ipotesi Sottogruppi definiti sulla base di fattori prognostici: debolezze • Molteplicità dei test statistici • Mancanza di potenza dei test statistici per verificare l’interazione • Risultati interpretabili solo in presenza di un risultato significativo a livello globale (la presenza d’interazione quando non c’è effetto del trattamento a livello complessivo dello studio implica interazione qualitativa) • Se la stratificazione è introdotta a posteriori: BIAS Principali Popolazioni di Analisi Studi di superiorità (generalmente end-point di efficacia) • Analisi primaria: – ITT • Analisi secondaria: – Completers (1) – Completers/Compliers (1) o (2) Studi di equivalenza (o non inferiorità) – Analisi di efficacia: • Analisi primaria: – ITT – Completers/Compliers (1) o (2) • Analisi secondaria: – Completers (1) – Analisi di sicurezza e tollerabilità: • Analisi primaria: – Safety • Analisi secondaria: – Completers/Compliers (1) Punto di vista dell’autorità regolatoria • ICH Harmonized tripartite Guideline E9. Statistical Principles for Clinical Trials. • [CPMP Working party on Efficacy of Medicinal Products. Note for guidance III/3630/92-EN: Biostatistical Methodology in clinical trials in applications for marketing authorizations for medicinal products. Statistics in Medicine 14; 1659-1682 (1995)] Punto di vista dell’autorità regolatoria (da ICH E9) • In confirmatory (and superiority) trials it is usually appropriate to plan to conduct both an analysis of the full set and a per protocol analysis (main sets) • The set of subjects whose data are to be included in the main analysis should be defined in the protocol and decisions should be guided by the following principles: minimize bias and avoid inflation of type I error (=The full set analysis is primary). Robustness of results to methods for evaluating withdrawals must be investigated. • Any differences between results obtained in the two analysis sets can be subject of explicit discussion and interpretation (sensitivity analysis) • Tutte le scelte “should be described and justified in the statistical section of the protocol” mentre considerazioni più dettagliate “can be deferred until the blind review of the data” • The full analysis set and the per protocol sets play different roles in superiority trials and in equivalence or non-inferiority trials Bibliografia su linee guida • S. Lange (2001). “The all randomized/full analysis set (ICH E9) - May patients be excluded from the analysis?” DIJ, 35; 881-891 • D. Gillings & G. Kock (1991). “The application of the principle of intention-to-treat to the analysis of clinical trials”. DIJ, 25; 441-424 Modified ITT (da ICH E9) “There are a limited number of circumstances that might lead to excluding randomized subjects from the full analysis, including: – the failure to satisfy major entry criteria; – the failure to take at least one dose of trial medication; – the lack of any data post randomization” Modified ITT: failure to satisfy major entry criteria (da ICH E9) “Subjects who fail to satisfy an entry criterion may be excluded from the analysis without the possibility of introducing bias only under the following circumstances: – the entry criterion was measured prior to randomization; – the detection of the relevant eligibility violations can be made completely objectively; – all subjects receive equal scrutiny for eligibility violations; – all detected violations of the particular entry criterion are excluded” Problemi/dubbi • Cosa significa “major”? Se la % di pazienti che non soddisfano i criteri “major” di inclusione è bassa, la loro inclusione/esclusione è ininfluente; se tale % è alta: – lo studio può avere problemi di qualità – la definizione di “major” è troppo ampia. • Caso particolare: studi clinici con agenti anti-infettivi • Cosa significa “objective detection”? • Se la selezione dei pazienti da escludere dall’analisi non poteva essere fatta al momento della randomizzazione, ciò significa che anche il medico che tratterà i pazienti sarà nelle stesse condizioni “Inclusion criteria are to help the physician decide who should enter the trial, not to tell the statistician who should enter the analysis” Stephen Senn Modified ITT: failure to take at least one dose of trial medication La linea guida E9 non dedica alcuna riflessione a questo aspetto, salvo dire “provided that the decision of whether or not to begin treatment could not be influenced by knowledge of the assigned treatment”. Problemi/dubbi • Come ci si comparta negli studi “open label” o “single blind”? • Non si può essere certi che il fatto che il trattamento non sia stato neppure iniziato non sia connesso con la conoscenza del trattamento => ciò ha un impatto sulla comparabilità tra i trattamenti Modified ITT: lack of any data post randomization La linea guida E9 riporta solo questa considerazione: “No analysis is complete unless the potential biases arising from their specific exclusions, or any others, are addressed” Problemi/dubbi • Solo ragioni tecniche sono sicuramente non correlate con il trattamento Modified ITT: poor study conduct in one center Questa ragione d’esclusione non è menzionata nella linea guida ICH E9 Problemi/dubbi Eppure, se il giudizio circa la qualità è dato in condizioni di cecità, questa ragione d’esclusione sembrerebbe lecita, visto che: – non ha impatto sulla randomizzazione e quindi sulla confrontabilità dei gruppi – non ha impatto sulla domanda clinica sottostante, in quanto l’obiettivo del trial clinico non è comunque quello di riflettere una scarsa qualità. Bibliografia su “Imputation Strategy” per analisi ITT • Little RJA. Journal of the Royal Statistical Society, Ser B, 41; 76-87 (1979) • Laird NM. Statistics in Medicine 7; 305-315 (1988) • Rubin D & Schenker N. Statistics in Medicine 10; 585-598 (1991) • Lavori P et al. Statistics in Medicine 14; 1913-1925 (1995) • Rubin D. Journal of the American Statistical Association 91; 473-489 (1996) Organizzazione delle attività formative prof.ssa Marinoni dr. Raschetti Le Competenze biostatistiche nell’ambito dei Comitati Etici Locali (Roma, 18 Marzo 2003) Gruppo di lavoro su: “Organizzazione delle attività formative” Prof.ssa A. Marinoni - Dr. Raschetti Al fine di organizzare attività formative per i biostatistici dei Comitati Etici, è necessario definire quali siano i bisogni formativi, e quindi le abilità e competenze necessarie ad un biostatistico per una corretta analisi di un protocollo di ricerca sottoposto al C.E. La metodologia proposta è quella dei gruppi di lavoro (mass. 5 persone per gruppo). Ad ogni gruppo sarà sottoposto un protocollo di ricerca presentato ad un C.E. approvato e non più confidenziale. Il gruppo esaminerà il protocollo secondo una delle griglie approntate, (una per ricerca sperimentale e una per ricerca osservazionale). Dalla discussione sull’analisi condotta emergeranno le carenze formative e le competenze richieste. Sarà quindi approntata una proposta di corso/corsi di formazione specifica Griglia per l’analisi critica del protocollo di un trial clinico 1) Background (razionale) (è motivata la necessità di fare la ricerca proposta allo stato attuale delle ricerche?) 2) Obiettivo/i - generale/i specifico/i (sono definiti in termini operativi l’obiettivo principale e quelli secondari? etc.) METODOLOGIA 3 Popolazione e Campione (base di campionamento, criteri di inclusione-esclusione, classificazione diagnostica) 4) Disegno dello studio - tipo di trial (efficacia-equivalenza, etc.) fase del trial tipo di controllo 5) Variabili raccolte e loro ruolo - end-point fattori prognostici fattori confondenti trattamento/i schemi di trattamento 6) Dimensioni dello studio (criteri per la definizione del n° di pazienti per braccio, etc.) 7) Metodi di analisi statistica (sono specificati i metodi di analisi? sono idonei, etc.) 8) Aspetti organizzativi (è garantito un idoneo coordinamento-controllo di qualità, regole di sospensione, etc.) 9) Aspetti economici (l’azienda in cui si fa la sperimentazione garantisce che il budget copra i costi?) 10) Foglio informativo per il paziente (è fornita una chiara e completa presentazione degli obiettivi della ricerca, dei rischi, etc.?) 11) Aspetti assicurativi (il medico legale e/o l’avvocato del C.E. ritengono l’assicurazione idonea per i pazienti e per i medici sperimentatori. Non solo per i dipendenti dello sponsor) 12) Aspetti etici - rilevanza del problema necessità della ricerca correttezza della metodologia eticità del gruppo di controllo (placebo o altro trattamento) accettabilità dei rischi (costo-beneficio) informazione corretta copertura dei costi, etc. Griglia per l’analisi critica del protocollo di uno studio osservazionale 1) Background (razionale) (è motivata la necessità di fare la ricerca proposta allo stato attuale delle ricerche?) 2) Obiettivo/i - generale/i specifico/i (sono definiti in termini operativi l’obiettivo principale e quelli secondari? etc.) METODOLOGIA 3 Popolazione e Campione (base di campionamento, criteri di inclusione-esclusione, classificazione diagnostica) 4) Disegno dello studio - tipo di trial (efficacia-equivalenza, etc.) fase del trial tipo di controllo 5) Variabili raccolte e loro ruolo - end-point fattori prognostici fattori confondenti trattamento/i schemi di trattamento 6) Dimensioni dello studio (criteri per la definizione del n° di pazienti per braccio, etc.) 7) Metodi di analisi statistica (sono specificati i metodi di analisi? sono idonei, etc.) 8) Aspetti organizzativi (è garantito un idoneo coordinamento-controllo di qualità, regole di sospensione, etc.) 9) Aspetti economici (l’azienda in cui si fa la sperimentazione garantisce che il budget copra i costi?) 10) Foglio informativo per il paziente (è fornita una chiara e completa presentazione degli obiettivi della ricerca, dei rischi, etc.?) 11) Aspetti assicurativi (se il caso) Griglia per la identificazione dei bisogni formativi (studi sperimentali) Competenze richieste 1) Background (razionale) 2) Obiettivo/i 3 Popolazione e Campione 4) Disegno dello studio 5) Variabili raccolte e loro ruolo 6) Dimensioni dello studio 7) Metodi di analisi statistica 8) Aspetti organizzativi 9) Aspetti economici 10) Foglio informativo per il paziente 11) Aspetti assicurativi 12) Aspetti etici Griglia per la identificazione dei bisogni formativi (studi osservazionali) Competenze richieste 1) Background (razionale) 2) Obiettivo/i 3 Popolazione e Campione 4) Disegno dello studio 5) Variabili raccolte e loro ruolo 6) Dimensioni dello studio 7) Metodi di analisi statistica 8) Aspetti organizzativi 9) Aspetti economici 10) Aspetti etici 11) Aspetti assicurativi (se il caso) Revisione delle linee guida dr.ssa Menniti-Ippolito dr.ssa Bacchieri REVISIONE DELLE LINEE GUIDA Le competenze biostatistiche nell’ambito dei Comitati Etici locali (Roma, 18 marzo 2003) Useful addresses • • • www.ich.org www.emea.eu.int www.fda.gov The European Agency for the Evaluation of Medicinal Products Pre-authorisation evaluation of medicines for human use EMEA London, 18 December 2002 CPMP/EWP/478/96 — Rev. 28 CPMP Efficacy Working Party Work programme 2003-2004 I. Meetings scheduled for 2003-2004 - II. Dates Plenary meeting/Number of day per meeting/number of member per meeting: • For 2003: 27-28 January; 8-9 April; 8-9 July and 7-8 October • For 2004: four two-days meeting (dates to be defined) Product related issues (such as support to Marketing Authorisation Assessment, Post-marketing Data Evaluation, Scientific Advice, Protocol Assistance). The following table provides, the expected number per year of contribution (number of involment in dossier) for Scientific Advice, Protocol Assistance, Product Assessment and Post-Authorisation issue (pharmacovigilance issue related to a product or a class of product). Expected contribution in Scientific Advice Efficacy Working Party contribution per year. 10 Expected contribution in Protocol Assistance 2 Expected contribution in Product Assessment 2 Expected contribution in Post-authorisation issue 2 III. CPMP Guidance documents 1. CNS/Pain: • Addendum on neuropathic pain to the Note for Guidance on clinical investigation of medicinal products for nociceptive Pain treatment (CPMP/EWP/612/00). Action: Concept paper expected in 1/2Q2003. • Note for Guidance on the evaluation of medicinal products for treatment of migraine (CPMP/EWP/788/01). Action: Released for 6-month consultation in September 2002 for comments by March 2003, expected to be finalised 3/4Q2003. • Appendix to the CPMP Note for guidance on the clinical investigation of medicinal products in the treatment of schizophrenia (CPMP/EWP/559/95), on methodology of clinical trials concerning the development of depot preparations of approved medicinal products in schizophrenia (CPMP/EWP/49/01). Action: Released for 6-month consultation in February 2002 for comments by August 2002 expected to be finalised 1/2Q2003. • Note for Guidance on Clinical Investigation of Medical Products in the Treatment of Generalised Anxiety Disorder. Action: Concept Paper on the revision of the existing guideline adopted in November 2002. Release for consultation expected in 3Q2003. 7 Westferry Circus, Canary Wharf, London, E14 4HB, UK Tel. (44-20) 74 18 84 00 Fax (44-20) 74 18 86 70 E-mail: [email protected] www.emea.eu.int ©EMEA 2002 Reproduction and/or distribution of this document is authorised for non commercial purposes only provided the EMEA is acknowledged • Note for Guidance on Clinical Investigation of Medical Products in the Treatment of Panic Disorder. Action: Concept Paper on the revision of the existing guideline adopted in November 2002. Release for consultation expected in 3Q2003. • Note for Guidance on Clinical Investigation of Medical Products in the Treatment of Obsessivecompulsive Disorder. Action: Concept Paper on the revision of the existing guideline adopted in November 2002. Release for consultation expected in 3Q2003. 2. Cardio-vascular: • Note for Guidance on the clinical development of Fibrinolytic medicinal products in the treatment of patients with ST segment elevation acute myocardial infarction (STEMI) (CPMP/EWP/967/01). Rap ES/DE Action: Released for 3-month consultation in November 2002 for comments by February 2003, expected to be finalised 3/4Q2003. • Addendum on acute cardiac failure to the CPMP Note for Guidance on clinical investigation of medicinal products in the treatment of acute cardiac failure (CPMP/EWP/1533/01). Action: Release for consultation expected 1/2Q2003 • Note for guidance on the evaiuation of medicinal products for the treatment of dyslipoproteinaemia (CPMP/EWP/5 12/01) Action: Release for consultation expected 1/2Q2003. • Note for guidance on the clinical investigation of antianginal medicinal products in stable angina pectoris. (CPMP/EWP/234/95). Action: Revision to be considered. 3. Rhumatology/Endocrinology: • Points to Consider on clinical investigation of medicinal products for treatment of Rheumatoid arthritis (CPMP/EWP/556/95-Rev. 1), Rapp-DE/SV/BE Action: Released for 3-month consultation in July 2002 for comments by October 2002. Finalisation expected 2Q2003. • Nfg on Clinical investigation of steroid contraceptives in women (CPMP/EWP/519/98). Action: Draft revision expected to be released for consultation 1Q2003 4. Gastro-intestinal: • Points to consider on irritable bowel syndrome (IBS) (CPMP/EWP/785/97) Action: Released for 3-month consultation in April 2002 for comments by July 2002. Finalisation expected 1/2Q2003. 5. Antibacterials/Anti-infectives/Vaccines: • Ptc document on the evaluation of new anti-fungal agents for invasive fungal infections (CPMP/EWP/1343/01). Action: Released for 6-month consultation in July 2002 for comments by January 2003. Finalisation expected 2/3Q2003 • Revision of NfG on evaluation of new anti-bacterial medicinal products (CPMP/EWP/558/95) and NfG on the pharmacodynamic section of the summary of product characteristics for antibacterial medicinal products (CPMP/EWP/96) Action: Release for consultation expected 1/2Q2003. • Note for Guidance on the clinical development of medicinal products for the treatment of HIV infection (CPMP/EWP/633/02). Action: Released for consultation in July 2002 for comments by October 2002. Finalisation expected 1/2Q2003 • Thiomersal: Muldisciplinary Ptc for the omission/removal of thiomersal from vaccines Multidisciplinary Guideline: Other involved WP: BWP, SWP, PhvWP 6. Biostatistical/methodological issues: ٧ • Points to consider on Biostatistical/methodological issues arising from CPMP discussion on licensing applications: Choice of Non-inferiority margin (CPMP/EWP/2158/99) Action: Release for consultation expected in 2003 ٧ • Points to consider on Biostatistical/methodological issues arising from CPMP discussion on licensing applications: Adjustment for baseline covariates (CPMP/EWP/2863/99) Action: Released for 3-month consultation in December 2001. Finalisation expected 1Q2003. ٧ • Points to consider on the use of statistical methods for flexible design and analysis of confirmatory clinical trials (CPMP/EWP/2459/02). Action: Released for 3-month consultation expected 1Q2003. ٧ • Points to consider on the use of statistical methods for flexible design and analysis of confirmatory clinical trials (CPMP/EWP/2459/02). Action: Released for 3-month consultation expected 1Q2003. 7. Pharmacokinetlc topics • Points to consider on clinical pharmacokinetic investigation of the pharmacokinetics of peptides and proteins (CPMP/EWP/226/02). Action: Release for consultation expected 2Q2003. • Note for guidance on the evaluation of the pharmacokinetics of medicinal products in patients with impaired renal function (CPMP/EWP/225/02). Action: Release for consultation expected 1Q2003. • Points to consider on the evaluation of the pharmacokinetics of medicinal products in the paediatric population (CPMP/EWP/968/02). Action: Release for consultation expected 1/2Q2003. • Note for guidance on the evaluation of the pharmacokinetics of medicinal products in patients with hepatic impairment (CPMP/EWP/2339/02). Action: Release for consultation expected 4Q2003. 8. Others: • Points to consider on the requirements for clinical documentation for Metered dose inhalers (CPMP/EWP/4151/00) Action: Released for 3-month consultation in January 2002 for comments by April 2002. Finalisation expected by 1/2Q2003. • Note for guidance on clinical investigation of medicinal products for the treatment of psoriasis (CPMP/EWP/2454/02). Action: Release for consultation expected in 2Q2003. • Points to consider on allergic rhino-conjuctivitis (CPMP/EWP/2455/02). Action: Release for 6-month consultation expected in 1/2Q2003. • Addendum to the Note For Guidance on Modified Release Oral and Transdermal Dosage Forms: Section 11 (PharmacoKinetic and Clinical Evaluation) (CPMP/EWP/280/96) on the clinical requirements of modified release products submitted as a line-extension of an existing marketing authorisation. Action: Release for consultation expected 1/2Q2003. • Points to consider on Xenogenic Cell Therapy (CPMP/3326/99). Multidisciplinary Guideline: Other involved WP: BWP, SWP, PhvWP. Action: EWP contribution to the BWP. Released for 6-month consultation in November 2002 for comments by May 2003. Finalisation expected 3Q2003. • Note for Guidance on Comparability of Medicinal Products containing biotechnology-derived proteins as active substance. Multidisciplinary Guideline: Other involved WP: BWP Action: Released for 6-month consultation in July 2002 • Nfg on the use of medicinal products during pregnancy: need for post-marketing data (CPMP/EWP/PhVWP/1417/01). Multidisciplinary Guideline: Other involved WP: PhVWP Action: Release for consultation expected 2003 • Nfg on risk assessment of medicinal products on human reproductive and development toxicities: from data to labelling. (CPMP/SWP/373/01). Multidisciplinary Guideline: Other involved WP: SWP Action: Concept paper adopted in June 2001. • NfG on the clinical requirements for locally applied, locally acting products containing known constituents (CPMP/EWP/239/95) Action: Revision to be considered. • NfG on clinical trials with haematopoietic growth factors for the prophylaxis of infection following myelosuppressive or myeloablative therapy (CPMP/EWP/555/95) Action: Revision to be considered. • NfG on fixed combination medicinal products (CPMP/EWP/240/95) Action: Revision to be considered. • MEDDEV guideline Action: EWP contribution in considreation III. ICH Guidelines and activities • E5: Ethnic Factors Action: Questions and answers document to be prepared for 1Q2003. • Clinical Guidance on Assessing QT Prolongation potential Action: Document to be prepared for 1Q2003. IV. EU Regulatory Activities • Notice to Applicant (CTD — ICH M4) Action: Follow-up of the implementation of the CTD. • Guideline on SPC Multidisciplinary Guideline: EC, PhWP, SWP, QWP, BWP, QRD group Action: Contribution to expected revision in 2003. • EC guidelines relating to the implementation of the Clinical Trial Directive Action: Follow-up of the EWP contribution. • Annex I of Directive 2001/83/EC Action: Follow-up of the EWP contribution V. Activities with external parties 1. Drug Regulatory Authorities Outside the EU (excluding ICH activities, already mentioned): - PERF III activities. - Liaison with FDA or other Agencies. 2. Meeting with Interested Parties (e.g. Learned Societies, Public health Stake Holders (Public health professionals, Patients’ organisations, ...), Pharmaceutical Industry Representatives). - Workshop with learned Societies to be considered once a year, in addition to improvement of written communication to favour Learned Societies’ input in draft EWP guidance. Meeting with EFPIA and/or other Pharmaceutical Industry Representative once/twice a year, upon request. - VI. Organisational matters 1. List of adopted organisational documents (e.g. mandate, template, SOP) - Recommendation for drafting CPMP/EWP clinical guidelines (CPMP/EWP/903/96, rev. 1), - Procedure for developing CPMP guidelines and points to consider documents (CPMP/2024/98), - Revision of the internal organisation of the EWP (dated February 2001), - Recommendation of the follow-up of EWP Points to consider/Note for guidance (CPMP/EWP/36/00, 16 March 2001), - Ongoing revision and update of the EWP Workplan, - EWP templates of concept paper, Points to consider and Note for Guidance with explanatory note (EMEA/8249/02). Efficacy Working Party (EWP) Adopted Guidelines CPMP/EWP/18/01 Note for Guidance on the Clinical Investigation of Medicinal Products in the Treatment of Urinary Incontinence in Women (CPMP adopted December 2002) CPMP/EWP/612/00 Note For Guidance on the Clinical Investigation of Medicinal Products for Treatment of Nociceptive Pain (CPMP adopted November 2002) CPMP/EWP/2922/01 Note for Guidance on the Clinical Investigation of Medicinal Products in the treatment of Asthma (CPMP adopted November 2002) CPMP/EWP/205/95 Revision 2 Note for Guidance on Evaluation of Anticancer Medicinal Products in Man (CPMP adopted September 2002) see also CPMP/EWP/569/02 draft Addendum on Paediatric Oncology (CVMP released for consultation September 2002) CPMP/EWP/282/02 Position Paper on the Regulatory Requirements for the Authorisation of Llowdose Modified Release asa Formulations in the Secondary Prevention of Cardiovascular Events (Final) CPMP/EWP/1080/00 Note For Guidance on Clinical Investigation of Medicinal Products in the Treatment of Diabetes Mellitus (CPMP adopted May 2002) CPMP/EWP/518/97 Revision 1 Note For Guidance on Clinical Investigation of Medicinal Products in the Treatment of Depression (CPMP adopted April 2002) CPMP/EWP/714/98 Revision 1 Note for Guidance on the Clinical Investigation of Medicinal Products in the Treatment of Peripheral Arterial Occlusive Disease (CPMP adopted April 2002) CPMP/180/95 Guideline for PMS Studies for Metered Dose Inhalers with New Propellants ٧ CPMP/EWP/2747/00 Note for Guidance on Co-ordinating Investigator Signature of Clinical Study Reports (Adopted October 2001) CPMP/EWP/561/98 Note for Guidance on Clinical Investigation of Medicinal Products for theTreatment of Multiple Sclerosis (Adopted July 2001) CPMP/EWP/QWP/1401/98 Note For Guidance on the Investigation of Bioavailability and Bioequivalence (Adopted July 2001) CPMP/EWP/567/98 Note for Guidance on Clinical Investigation of Medicinal Products for Bipolar Disorder (CPMP adopted April 2001) CPMP/EWP/552/95 Revision 1 Note for Guidance on Post Menopausal Osteoporosis in Women (CPMP adopted January 2001) CPMP/EWP/566/98 Revision 1 Note for Guidance on Clinical Investigation of Medicinal Products in the Treatment of Epilectic Disorders (CPMP adopted November 2000) CPMP/EWP/519/98 Note for Guidance on Clinical Investigation of Steroid Contraceptives in Women CPMP/EWP/235/95 Revision 1 Note for Guidance on the Clinical Investigation of Medicinal Products in the Treatment of Cardiac Failure (CPMP adopted Dec. 99) CPMP/EWP/563/98 Note for Guidance on Clinical Investigation of Medicinal Products for the Treatment of Venous Thromboembolic Disease (CPMP adopted Dec. 99) CPMP/EWP/280/96 Note For Guidance on Modified Release Oral and Transdermal Dosage Forms: Section II (PharmacoKinetic and Clinical Evaluation) CPMP/EWP/463/97 Note for guidance on Clinical Evaluation of New Vaccines CPMP/EWP/563/95 Note for guidance on Clinical Investigation of Medicinal Products in the Treatment of Parkinson's Disease CPMP/EWP/238/95 Revision 1 Note for Guidance on Clinical Investigation on Medicinal Products in the Treatment of Hypertension (CPMP adopted May 97, revised November 98) CPMP/EWP/559/95 Note for guidance on the Clinical Investigation of Medicinal Products in the Treatment of Schizophrenia (CPMP adopted Feb. 98) CPMP/EWP/281/96 Note for Guidance on the Clinical Investigation of Drug used for Weight Control (CPMP adopted Dec. 97) CPMP/EWP/560/95 Note for Guidance on the Investigation of Drug Interactions (CPMP adopted Dec. 97) CPMP/EWP/553/95 Note for Guidance on Medicinal Products in the Treatment of Alzheimer's Disease (CPMP adopted July 97) CPMP/EWP/520/96 Note for Guidance on the Pharmacodynamic section of the SPC for AntiBacterial Medicinal Products (CPMP adopted June 97) CPMP/EWP/234/95 Note for guidance on the clinical investigation of anti-anginal medicinal products in stable angina pectoris CPMP/EWP/558/95 Note for Guidance on Evaluation of new anti-Bacterial Medicinal Products (CPMP adopted April 97) CPMP/EWP/462/95 Note for Guidance on Clinical Investigation of Medicinal Products in Children (CPMP adopted March 97) CPMP/EWP/240/95 Note for Guidance on Fixed Combination Medicinal Products (CPMP adopted April. 96) CPMP/EWP/555/95 Note for Guidance on Clinical trials with Haematopoietic Growth factors for the Prophylaxis of Infection following Myelosuppressive or Myeloablative Therapy (CPMP adopted March 96) CPMP/EWP/237/95 Note for Guidance on Antiarrhythmics (CPMP adopted Nov.95) CPMP/EWP/239/95 Note for Guidance on the Clinical Requirements for Locally Applied, Locally Acting Products containing Known Constituents (CPMP adopted Nov.95) • Workplan • • Concept Papers • Points to Consider • Draft Guidelines • Adopted Guidelines • © 1995-2003 EMEA Send all queries regarding the Web content to: [email protected] Send all queries regarding the Web functionality to: EMEAwebservices Efficacy Working Party (EWP) Draft Guidelines CPMP/EWP/967/01 Note for Guidance on the Evaluation of Medicinal Products indicated for Thrombolysis in Acute Myocardial Infarction (AMI) (Released for consultation November 02) CPMP/EWP/788/01 Note for Guidance on the Clinical Investigation of Medicinal Products for treatment of Migraine (Released for consultationSeptember 02) CPMP/3097/02 Note for Guidance Consultation on Comparability of Medicinal Products containing Biotechnology-deriverd Proteins as Drug Substance (Released for consultation July 02) CPMP/EWP/633/02 Note for Guidance on Clinical Development of Medicinal Products for the Treatment of HIV Infection (Released for consultation July 02) CPMP/EWP/49/01 Appendix to the Committee for Proprietary Medicinal Products (CPMP) Note for Guidance on the Clinical Investigation of Medicinal Products in the Treatment of Schizophrenia, on the Methodology of Clinical Trials concerning the Development of Depot Preparations of Approved Medicinal Products in Schizophrenia (Released for consultation February 02) • Workplan • • Concept Papers • Points to Consider • Draft Guidelines • Adopted Guidelines • © 1995-2002 EMEA Send all queries regarding the Web content to: [email protected] Send all queries regarding the Web service to: Webmaster Efficacy Working Party (EWP) Points to Consider ٧ ٧ ٧ ٧ ٧ CPMP/EWP/908/99 CPMP Points to Consider on Multiplicity issues in Clinical Trials (CPMP Adopted September 2002) CPMP/EWP/1343/01 Points to Concider of new Anti-Fungal Agents for Invasive Fungal Infections (Released for consultation Julyl 02) CPMP/EWP/785/97 Points to Consider on the Evaluation of Medicinal Products for the Treatment of Irritable Bowel Syndrome (Released for consultation April 02) CPMP/602/95 Rev. 3 Points to consider on the Assessment of Anti-HIV Medicinal Products (Adopted by CPMP in December 2001) CPMP/EWP/4151/00 Points to Consider on the Requirements for Clinical Documentation for Metered Dose Inhalers (MDI)(Released for consultation January 02) CPMP/EWP/2863/99 Points to Consider on Adjustment for baseline Covariates (Released for Consultation December 2001) CPMP/EWP/1776/99 Points to Consider on Missing Data ( Adopted November 2001) CPMP/EWP/1119/98 Points to Consider on the Evaluation of the diagnostic agents ( Adopted November 2001) CPMP/EWP/560/98 Points to Consider on Clinical Investigation of Medicinal Products for theTreatment of Acute Stroke ( Adopted September 2001) CPMP/EWP/2284/99 Points to Consider on Clinical Investigation of Medicinal Products for the Management of Crohn's Disease (adopted by CPMP June 2001) CPMP/2330/99 Points to Consider on Application with 1.) Meta-analyses and 2.) One Pivotal study (adopted by CPMP May 2001) CPMP/EWP/565/98 Points to Consider on Clinical Investigation of Medicinal Products for theTreatment of Amyotrophic Lateral Sclerosis (Adopted October 2000) CPMP/EWP/482/99 Points to Consider on Switching between Superiority and Noninferiority (Adopted July 2000) CPMP/EWP/2655/99 Points to Consider on Pharmacokinetics and Pharmacodynamics in the Development of Antibacterial Medicinal Products (Adopted July 2000) CPMP/EWP/707/98 Points to Consider on Clinical Investigation of Medicinal Products fo Prophylaxis of Intra- and Post- operative Venous Thromboembolic Risk (CPMP approved June 2000) CPMP/EWP/570/98 Points to Consider on Clinical Investigation of New Medicinal Products for the treatment of Acute Coronary syndrome (ACS) without persistent ST-Segment Elevation CPMP/EWP/197/99 Points to Consider concerning Endpoints in Clinical Studies with Haematopoietic Growth Factors for Mobilisation of Autologous Stem Cells CPMP/EWP/863/98 Points to Consider on Wording of Helicobacter Pylori Eradication Therapy in selected SPC Sections CPMP/EWP/562/98 Points to Consider on Clinical Investigation of Medicinal Products in the Treatment of Patients with Chronic Obstructive Pulmonary Disease (COPD) CPMP/EWP/556/95 Points to Consider on the Clinical Investigation of Slow-Acting Anti-Rheumatic Medicinal Products in Rheumatoid Arthritis CPMP/EWP/784/97 Points to Consider on Clinical Investigation of Medicinal Products used in the Treatment of Osteoarthritis CPMP/EWP/021/97 Points to Consider on Hormone Replacement Therapy.(of 19 November 1997) CPMP/EWP/504/97 Points to Consider on Clinical investigation of Medicinal Products in the Treatment of Patients with Acute Respiratory Distress Syndrome.(of 9 October 1997) • Workplan • • Concept Papers • Points to Consider • Draft Guidelines • Adopted Guidelines • © 1995-2003 EMEA Send all queries regarding the Web content to: [email protected] Send all queries regarding the Web functionality to: EMEAwebservices Efficacy Working Party (EWP) Concept Papers ٧ ٧ CPMP/EWP/4279/02 Concept Paper on the Development of a CPMP Note for Guidance on Clinical Investigation of Medicinal Products for the Treatment of Obsessive Compulsive Disorder CPMP/EWP/4280/02 Concept Paper on the Development of a CPMP Note for Guidance on Clinical Investigation of Medicinal Products for the Treatment of Panic Disorder CPMP/EWP/4284/02 Concept Paper on the Development of a CPMP Note for Guidance on Clinical Investigation of Medicinal Products for the Treatment of General Anxiety Disorder CPMP/EWP/2459/02 Concept Paper on the Development of a CPMP Points to Concider on Methodological Issues in Confirmatory Clinical Trials with Flexible Design and Analysis Plan CPMP/EWP/2339/02 Concept Paper on the Development of a CPMP Note for Guidance on Evaluation of the Pharmacokinetics of Medicinal Products in Patients with Hepatic Impairment CPMP/EWP/2454/02 Concept Paper on the Development of a CPMP Note for Guidance on Clinical Investigation of medicinal products ot the Treatment of Psoriasis CPMP/EWP/2455/02 Concept Paper on the Development of a CPMP Points to Consider on Allergic Rhino-conjunctivitis CPMP/EWP/968/02 Concept Paper on the Development of a CPMP Points to Consider on the Evaluation of the Pharmacokinetics of Medicinal Products in the Paediatric Population CPMP/EWP/226/02 Concept Paper on the Development of a CPMP NfG on the Clinical Pharmacokinetic investigation of the Pharmacokinetics of Peptides and Proteins CPMP/EWP/225/02 Concept Paper on the Development of a CPMP NfG on the Evaluation of the Pharmacokinetics of Medicinal Products in Patients with Impaired Renal Function CPMP/EWP/1412/01 Concept Paper on the Development of the Revision of the CPMP NfG on Evaluation of New Anti-bacterial Medicinal Products (CPMP/EWP/558/95) and the CPMP NfG on the Pharmacodynamic Section of the SPC for Anti-bacterial Medicinal Products (CPMP/EWP/520/96) CPMP/EWP/2991/01 Concept Paper on the Development of an Addendum the Clinical Requirements of Modified Release Medicinal Products submitted as a Line Extension of an existing Marketing Authorization to the CPMP Note for Guidance on Modified Release Oral and Transdermal Dosage Forms: Section II (Pharmacokinetic and Clinical Evaluation)(CPMP/EWP/280/96) CPMP/EWP/1533/01 Concept Paper on the Development of an Addendum on Acute Cardiac Failure to the CPMP Note for Guidance on Clinical Investigation of Medicinal Products in the Treatment of Acute cardiac Failure CPMP/EWP/PHVWP/1417/01 Concept Paper on the Development of a Committee for Proprietary Medicinal Products (CPMP) Note for Guidance on the Use of Medicinal Products during Pregnancy: Need for Post-Marketing Data CPMP/EWP/512/01 Concept Paper on the Development of a Committee for Proprietary Medicinal Products (CPMP) Note for Guidance on the Evaluation of Medicinal Products for the treatment of Dyslipoproteinaemia CPMP/EWP/2158/99 Concept Paper on the Development of a Committee for Proprietary Medicinal Products (CPMP) Points to Consider on Biostatistical/Methodological issues arising from recent CPMP discussions on Licensing Applications: Choice of Delta • Workplan • • Concept Papers • Points to Consider • Draft Guidelines • Adopted Guidelines • © 1995-2003 EMEA Send all queries regarding the Web content to: [email protected] Send all queries regarding the Web service to: Webmaster ICH • • • INTERNATIONAL CONFERENCE OF HARMONIZATION OF TECHNICAL REQUIREMENTS FOR REGISTRATION OF PHARMACEUTICALS FOR HUMAN USE. IT IS A UNIQUE PROJECT THAT BRINGS TOGETHER THE REGULATORY AUTHORITIES OF EUROPE, JAPAN, UNITED STATES AND EXPERTS FROM THE PHARMACEUTICAL INDUSTRY IN THE THREE REGIONS TO DISCUSS SCIENTIFIC AND TECHNICAL ASPECTS OF PRODUCT REGISTRATION. THE PURPOSE IS TO MAKE RECOMMENDATIONS ON WAYS TO ACHIEVE GREATER HARMONIZATION IN THE INTERPRETATION AND APPLICATION OF TECHNICAL GUIDELINES AND REQUIREMENTS FOR PRODUCT REGISTRATION IN ORDER TO REDUCE OR OBVIATE THE NEED TO DUPLICATE THE TESTING CARRIED OUT DURING THE RESEARCH AND DEVELOPMENT OF NEW MEDICINES. HISTORY OF ICH • • • • • TRIGGERS FOR SETTING UP THE PRODUCT AUTHORIZATION SYSTEM: - USA => TRAGIC MISTAKE IN THE FORMULATION OF A CHILDREN’S SYRUP IN THE 1930s (=>FDA) - JAPAN => NEED FELT IN THE 1950s (=> MHLW) - EUROPE => THALIDOMIDE TRAGEDY IN THE 1960s (=> EMEA) THE 1960s AND 1070s SAW A RAPID INCREASE IN LAWS, REGULATIONS AND GUIDELINES FOR REPORTING AND EVALUATING THE DATA ON SAFETY, QUALITY AND EFFICACY OF NEW MEDICINAL PRODUCTS. AT THE WHO CONFERENCE OF DRUG REGULATORY AUTHORITIES (ICDRA) IN PARIS IN 1989 SPECIFIC PLANS FOR ACTION BEGAN TO MATERIALIZE THE BIRTH OF ICH TOOK PLACE AT A MEETING IN APRIL 1990, HOSTED BY EFSPIA IN BRUSSELS THE MEETING AT SAN DIEGO IN 2000 MARKS THE END OF 10 YEARS OF ACTIVITY. STRUCTURE OF ICH • • • • ICH STEERING COMMITTEE: ESTABLISHED IN 1990 HAS MET AT LEAST TWICE A YEAR WITH LOCATION ROTATING BETWEEN THE TRHEE REGIONS. SIX-PARTY EXPERT WORKING GROUPS (EWG): FOR EVERY NEW TOPIC, EACH OF THE SIX ICH PARTIES (EC, EFPIA, MHLW, JPMA, FDA, PhRMA) DESIGNATE A TOPIC LEADER, WHO WILL PARTICIPATE IN THE EWG MEETINGS SOMETIMES MEMBERSHIP OF EWG CAN BE EXTENDED TO OTHER INTERESTED PARTIES THREE OBSERVERS THAT NOMINATE AN EXPERT TO THE EWG TOPICS FOR HARMONIZATION ARE DEVIDED INTO: SAFETY QUALITY EFFICACY MAJOR TOPICS: MINOR TOPICS: - ABBREVIATED - FULL ICH MAINTENANCE PROCESS PROCESS BASED ON A FIVE-STEP APPROACH FULL ICH PROCESS • • • • • STEP 1: CONSENSUS BUILDING - SIGN-OFF BY EXPERT WORKING GROUPS MEMBERS STEP 2: START OF REGULATORY ACTION - REACHED WHEN THE STEERING COMMITTEE AGREES, ON THE BASIS OF THE REPORT FROM THE EWG, THAT THERE IS SUFFICIENT SCIENTIFIC CONSENSUS ON THE TECHNICAL ISSUES FOR THE GUIDELINE TO PROCEED TO THE NEXT STAGE OF REGULATORY CONSULTATION STEP 3: REGULATORY CONSULTATION - THE GUIDELINE LEAVES THE ICH PROCESS AND BECOMES THE SUBJECT OF NORMAL WIDE-RANGING CONSULTATION IN THE THREE REGIONS. IT IS PRINTED AS A DRAFT (BY CPMP, FDA AND MHLW) FOR INTERNAL AND EXTERNAL REVIEW STEP 4: ADOPTION OF A TRIPARTITE HARMONIZED TEXT - THE GUIDELINE RETURNS TO THE ICH FORUM. IF BOTH REGULATORY AND INDUSTRY PARTIES ARE SATISFIED THAT THE CONSENSUS ACHIEVED AT STEP 2 IS NOT SUBSTANTIALLY ALTERED AS RESULT OF THE CONSULATION, THE TEXT IS ADOPTED BY THE STEERING COMMITTEE STEP 5: IMPLEMENTATION International Conference on Harmonization (ICH) Efficacy - Adopted Guidelines ٧ ٧ ٧ ٧ ٧ ٧ Topic E 2B(M) Step 5 Modification Note for Guidance on Clinical Safety Data Management: Data Elements for Transmission of Individual Case Safety Reports (ICH ICSR DTD Version 2.3)(CPMP/ICH/287/95 - Mod. released foir information November 2000) Topic E11 Step 4 Note for Guidance on Clinical Investigation of Medicinal Products in the Paediatric Population.(CPMP/ICH/2711/99 - adopted July 2000) Topic E10 Step 4 Note for Guidance on Choice of Control Group for Clinical Trials (CPMP/ICH/364/96 - adopted July 2000) Topic E9 Step 4 Note for Guidance on Statistical Principles for Clinical Trials.(CPMP/ICH/363/96 adopted Mar.98) Topic E5 Step 4 Note for Guidance on Ethnic Factors in the Acceptability of Foreign Clinical Data.(CPMP/ICH/289/95 - adopted Mar.98) Topic E8 Step 4 Note for Guidance on General Considerations for Clinical Trials(CPMP/ICH/291/95 - adopted Sept. 97) Topic E6 Step 5 Note for Guidance on Good Clinical Practice(CPMP/ICH/135/95 - adopted July 96) Explanatory Note and Comments to CPMP/ICH/135/95 Topic E2C Step 4 Note for Guidance on Clinical Safety Data Management: Periodic Safety Update Reports for Marketed Drugs (CPMP/ICH/288/95 - adopted December 96) Topic E2A Step 5 Note for Guidance on Good Clinical Safety Data Management: Definitions and Standards for Expedited Reporting (CPMP/ICH/377/95 - adopted November 94) Topic E1A Step 5 Note for Guidance on Population Exposure: The extent of Population Exposure to assess Clinical Safety (CPMP/ICH/375/95 adopted November 94) Topic E4 Step 5 Note for Guidance on Dose Response Information to support Drug Registration (CPMP/ICH/378/95 - adopted May 94) Topic E7 Step 5 Note for Guidance on Studies in support of Special Populations: Geriatrics( CPMP/ICH/379/95 - adopted Sept. 93) Topic E3 Step 4 Note for Guidance on Structure and Content of Clinical Study Reports(CPMP/ICH/137/95 - adopted Dec. 95) Annex I Annex II Annex III Annex IVa Annex IVb Annex V Annex VI Annex VII Annex VIII © 1995-2001 EMEA Send all queries regarding the Web content to: [email protected] Send all queries regarding the Web service to: Webmaster International Conference on Harmonization (ICH) Efficacy - Draft Guidelines Topic V1* Clinical Safety Data Management Periodic Safety Update Reports for Marketed Drugs (CPMP/ICH/4679/02 - released for consultation Sept.2002) (Addendum to ICH E2C) Topic E 12 A (Draft Consensus) Principles for Clinical Evaluation of new Antihypertensive Drugs (CPMP/ICH/541/00 - released for consultation Jun.00) * Provisional Designation © 1995-2002 EMEA Send all queries regarding the Web content to: [email protected] Send all queries regarding the Web service to: Webmaster Guidance Documents Guidance documents represent the Agency's current thinking on a particular subject. They do not create or confer any rights for or on any person and do not operate to bind FDA or the public. An alternative approach may be used if such approach satisfies the requirements of the applicable statute, regulations, or both. For information on a specific guidance document, please contact the originating office. Most of these documents are in Adobe Acrobat format , also known as PDF. The free upgrade to Adobe Acrobat 4.0 or higher is recommended, especially if you have difficulty opening any of the documents below. Another method of obtaining guidance documents is through the Division of Drug Information. [Accessibility] Search Clear CDER Guidance Documents Enter words or phrases, separated by commas (See Help for search tips) • • • • • FDA's Good Guidance Practices regulation of September 19, 2000. Optional Format: PDF. Comprehensive List of Guidance Documents (3/11/2003) Guidance Agenda: Guidances CDER is Planning to Develop During Fiscal Year 2003 (10/21/2002) New/Revised/Withdrawn List for 2000 New/Revised/Withdrawn List (5/24/2001) (9/23/2002) Advertising 1. 2. 3. Aerosol Steroid Product Safety Information in Prescription Drug Advertising and Promotional Labeling (Issued 12/1997, Posted 1/12/1998) Consumer-Directed Broadcast Advertisements [HTML] or [PDF] (Issued 8/1999, Posted 8/6/1999) Questions and Answers (Posted 8/6/1999) Industry-Supported Scientific and Educational Activities [HTML] or [PDF] (Issued 12/3/1997, Posted 12/4/1997) Advertising Draft 1. Accelerated Approval Products: Submission of Promotional Materials 2. (Issued 1/1999, Product Name Placement, Size, and Prominence in Advertising and Promotional Labeling Posted 3/12/1999) Promoting Medical Products in a Changing Healthcare Environment; I. Medical Product Promotion by 3. 4. (Posted 3/26/1999) Healthcare Organizations or Pharmacy Management Companies (PBMs) (Issued 12/1997. Posted 1/5/1998) Using FDA-Approved Patient Labeling in Consumer-Directed Print Advertisements [HTML] or [PDF] (Issued 4/2001, Posted 4/20/2001] Biopharmaceutics 1. 2. Bioanalytical Method Validation [HTML] or [PDF] (Issued 5/2001, Posted 5/22/2001) Bioavailability and Bioequivalence Studies for Orally Administered Drug Products - General Considerations [Word] or [PDF] (Issued 3/2003, Posted 3/19/2003) 3. Cholestyramine Powder in Vitro Bioequivalence (Intermin Guidance) 4. Clozapine Tablets in Vivo Bioequivalence and in Vitro Dissolution Testing 10/15/1998) (Issued 11/15/1996, Reposted 5. Corticosteroids, Dermatologic (topical) In Vivo 6. Dissolution Testing of Immediate Release Solid Oral Dosage Forms or WordPerfect 6.x Version (Issued 8/1997, Posted 8/25/1997) Extended Release Oral Dosage Forms: Development, Evaluation, and Application of In Vitro/In Vivo 7. 8. (Issued 6/2/1995, Posted 3/6/1998) Correlations (Issued 9/1997, Posted 9/26/1997) Food-Effect Bioavailability and Fed Bioequivalence Studies [Word] or [PDF] (Issued 12/2002, Posted 1/30/2003) (Issued 6/27/1989, Posted 3/2/1998) 9. Metaproterenol Sulfate and Albuterol Metered Dose Inhalers In Vitro 10. Phenytoin/Phenytion Sodium (capsules, tablets, suspension) In Vivo Bioequivalence and In Vitro Dissolution Testing (Issued 3/4/1994, Posted 3/2/1998) 11. Potassium Chloride (slow-release tablets and capsules) In Vivo Bioequivalence and In Vitro Dissolution Testing (Revised 6/6/1994, Posted 6/22/1998) 12. Statistical Approaches to Establishing Bioequivalence [HTML] or [PDF] (Issued 2/2001, Posted 2/1/2001) 13. Waiver of In Vivo Bioavailability and Bioequivalence Studies for Immediate-Release Solid Oral Dosage Forms Based on a Biopharmaceutics Classification System. Optional Format: PDF. (Issued 8/2000, Posted 8/31/2000) Biopharmaceutics (Draft) 1. 2. 3. 4. Bioavailability and Bioequivalence Studies for Nasal Aerosols and Nasal Sprays for Local Action [Word] or [PDF] (Posted 4/2/2003) o Statistical Information from the June 1999 Draft Guidance and Statistical Information for In Vitro Bioequivalence Data (Posted 4/11/2003) Conjugated Estrogens, USP-LC-MS Method for Both Qualitative Chemical Characterization and Documentation of Qualitative Pharmaceutical Equivalence [HTML] or [PDF] (Issued 3/6/2000, Posted 3/6/2000) In Vivo Bioequivalence Studies Based on Population and Individual Bioequivalence Studies (Issued 12/10/1997, Posted 12/10/1997) Bioequivalence Studies Data and Detailed Statistical Methodology (Posted 3/2/1998) Potassium Chloride Modified-Release Tablets and Capsules: In Vivo Bioequivalence and In Vitro Dissolution Testing (Issued 8/2002, Posted 8/6/2002) Chemistry 1. 2. 3. 4. 5. 6. 7. 8. 9. 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Postmarketing Adverse Experience Reporting for Human Drug and Licensed Biological Products: Clarification of What to Report or WordPerfect 6.x version (Issued 8/27/1997, Posted 8/27/1997) 35. Postmarketing Reporting of Adverse Drug Experiences (Issued 3/1992, Posted 3/2/1998) 36. Preclinical Development of Immunomodulatory Drugs for Treatment of HIV Infection and Associated Disorders (Reposted 1/21/1999) 37. Preparation of Investigational New Drug Products (Human and Animal) (Issued 11/1992, Posted 3/2/1998) 38. Providing Clinical Evidence of Effectiveness for Human Drug and Biological Products (Issued 5/14/1998, Posted 5/14/1998) 39. Prussian Blue Drug Products — Submitting a New Drug Application [Word] [PDF] (Issued 1/2003, Posted 2/4/2003) 40. Study and Evaluation of Gender Differences in the Clinical Evaluation of Drugs 3/2/1998) 41. Study of Drugs Likely to be used in the Elderly (Issued 7/22/1993, Posted (Issued 11/1989, Posted 3/2/1998) 42. Submission of Abbreviated Reports and Synopses in Support of Marketing Applications [HTML] or [PDF] (Issued 8/1999, Posted 9/13/1999) ٧ Clinical/Medical (Draft) 1. 2. 3. 4. 5. 6. 7. Allergic Rhinitis: Clinical Development Programs for Drug Products [HTML] or [PDF] (Issued 6/2000, Posted 6/20/2000) Available Therapy [HTML] or [PDF] (Posted 2/6/2002) Chronic Cutaneous Ulcer and Burn Wounds — Developing Products for Treatment [HTML] or [PDF] (Issued 6/2000, Posted 6/27/2000) Clinical Development Programs for Drugs, Devices, and Biological Products Intended for the Treatment of Osteoarthritis [Word] or [PDF] (Issued 7/07/1999, Posted 7/14/1999) Clinical Evaluation of Lipid-Altering Agents (Issued 10/1990, Posted 2/18/1998) Clinical Evaluation of Weight-Control Drugs (9/24/1996, Posted 2/18/1998) Clinical Trial Sponsors On the Establishment and Operation of Clinical Trial Dada Monitoring Committees [HTML] or [PDF] (11/15/2001) 8. 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(Posted 3/2/1998) Letter describing efforts by the CDER and the ORA to clarify the responsibilities of CDER chemistry review scientists and ORA field investigators in the new and abbreviated drug approval process in order to reduce 6. duplication or redundancy in the process (Posted 3/2/1998) Letter on incomplete Abbreviated Applications, Convictions Under GDEA, Multiple Supplements, Annual Reports for Bulk Antibiotics, Batch Size for Transdermal Drugs, Bioequivalence Protocols, Research, 7. Deviations from OGD Policy (Posted 3/2/1998) Letter on the Provision of new information pertaining to new bioequivalence guidelines and refuse-to-file letters (Posted 3/2/1998) 8. Letter on the provision of new procedures and policies affecting the generic drug review process 3/2/1998) (Posted 9. Letter on the request for cooperation of regulated industry to improve the efficiency and effectiveness of the generic drug review process, by assuring the completeness and accuracy of required information and data submissions (Posted 3/2/1998) 10. Letter on the response to 12/20/1984 letter from the Pharmaceutical Manufacturers Association about the Drug Price Competition and Patent Term Restoration Act (Posted 3/2/1998) 11. Letter to all ANDA and AADA applicants about the Generic Drug Enforcement Act of 1992 (GDEA), and the Office of Generic Drugs intention to refuse-to-file incomplete submissions as required by the new law (Posted 3/2/1998) 12. Letter to regulated industry notifying interested parties about important detailed information regarding labeling, scale-up, packaging, minor/major amendment criteria and bioequivalence requirements (Posted 3/2/1998) 13. Major, Minor, and Telephone Amendments to Abbreviated New Drug Applications [PDF] (Issued 12/2001, Posted 12/20/2001) 14. Organization of an ANDA (Issued 2/1999, 3/2/1999) 15. Revising ANDA Labeling Following Revision of the RLD Labeling [HTML] or [PDF] (Issued 4/26/2000, 4/26/2000) 16. Skin Irritation and Sensitization Testing of Generic Transdermal Drug Products [HTML] or [PDF] (Issued 12/1999, Posted 2/3/2000) 17. Variations in Drug Products that May Be Included in a Single ANDA (Issued 12/1998, Posted 1/26/1999) Generics (Draft) 1. 2. ANDAs: Impurities in Drug Products (Issued 12/1998, Posted 1/5/1999) Content and Format of an Abbreviated New Drug Application (ANDA) - Positron Emission Tomography (PET) Drug Products With specific information for ANDAs for Fludeoxyglucose F18 Injection (Issued 4/1997, Posted 3. 4. Handling and Retention of BA and BE Testing Samples (Issued 8/2002, Posted 8/20/2002) Potassium Chloride Modified-Release Tablets and Capsules: In Vivo Bioequivalence and In Vitro Dissolution Testing [PDF] (Issued 8/2002, Posted 8/6/2002) 4/23/1997) Good Review Practices (GRPs) 1. Pharmacology/Toxicology Review Format [PDF] (Posted 5/9/2001) Good Review Practices (GRPs) (Draft) 1. Conducting a Clinical Safety Review of a New Product Application and Preparing a Report on the Review (11/1996) Industry Letters 1. Continuation of a series of letters communicating interim and informal generic drug policy and guidance. Availability of Policy and Procedure Guides, and further operational changes to the generic drug review 2. program (Posted 3/2/1998) Fifth of a series of letters providing informal notice about the Act, discussing the statutory mechanism by which 3. ANDA applicants may make modifications in approved drugs where clinical data is required (Posted 3/2/1998) Fourth of a series of letters providing informal notice to all affected parties about policy developments and interpretations regarding the Act. Three year exclusivity provisions of Title I (Posted 3/2/1998) 4. Implementation of the Drug Price Competition and Patent Term Restoration Act. Preliminary Guidance (Posted 3/2/1998) 5. 6. Implementation Plan USP injection nomenclature (Posted 3/2/1998) Seventh of a series of letters about the Act providing guidance on the "130-day exclusivity" provision of section 7. 505(j)(4)(B)(iv) of the FD&C (Posted 3/2/1998) Sixth of a series of informal notice letters about the Act discussing 3-and 5-year exclusivity provisions of sections 505(c)(3)(D) and 505(j)(4)(D) of the FD&C Act 8. (Posted 3/2/1998) Supplement to 10/11/1984 letter about policies, procedures and implementation of the Act (Q&A format) (Posted 3/2/1998) 9. Third of a series of letters regarding the implementation of the Act 10. Year 2000 Letter from Dr. Janet Woodcock (10/19/98) (Posted 3/2/1998) International Conference on Harmonisation Safety 1. S1A The Need for Long-term Rodent Carcinogenicity Studies of Pharmaceuticals 2. S1B Testing for Carcinogenicity of Pharmaceuticals 3. 4. S1C Dose Selection for Carcinogenicity Studies of Pharmaceuticals S1C(R) Guidance on Dose Selection for Carcinogenicity Studies of Pharmaceuticals: Addendum on a Limit 5. S2A Specific Aspects of Regulatory Genotoxicity Tests for Pharmaceuticals 6. S2B Genotoxicity: A Standard Battery for Genotoxicity Testing of Pharmaceuticals Posted 5/4/1998) Dose and Related Notes (Issued 2/28/1998, Posted 3/24/1998) (Issued 12/4/1997, Posted 12/11/1997) (Issued 11/21/1997, 7. S3A Toxicokinetics: The Assessment of Systemic Exposure in Toxicity Studies 8. 9. S3B Pharmacokinetics: Guidance for Repeated Dose Tissue Distribution Studies S4A Duration of Chronic Toxicity Testing in Animals (Rodent and Nonrodent Toxicity Testing) [PDF] or [Text] Posted 6/25/99 10. S5A Detection of Toxicity to Reproduction for Medicinal Products (Issued 9/1994, Posted 4/23/1997) 11. S5B Detection of Toxicity to Reproduction for Medicinal Products: Addendum on Toxicity to Male Fertility (Issued 11/1997, Posted 12. 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M3 Nonclinical Safety Studies for the Conduct of Human Clinical Trials for Pharmaceuticals (Issued 11/1997, Posted 11/25/1997) M4: Common Technical Document for the Registration of Pharmaceuticals for Human Use (Posted 10/15/2001) o M4: Organization of the CTD [HTML] or [PDF] M4: The CTD -- General Questions and Answers [WORD] or [PDF] (Issued 2/2003, Posted 2/3/2003) o M4: The CTD -- Quality [HTML] or [PDF] o M4: The CTD -- Efficacy [HTML] or [PDF] M4: The CTD -- Efficacy Questions and Answers [WORD] or [PDF] (Issued 1/2003, Posted 2/4/2003) o M4: The CTD -- Safety [HTML] or [PDF] o M4: The CTD -- Safety Appendices [HTML] or [WORD] or [PDF] M4: The CTD -- Safety Questions and Answers [WORD] or [PDF] (Issued 2/2003, Posted 2/4/2003) 3. Efficacy 1. E1A The Extent of Population Exposure to Assess Clinical Safety: For Drugs Intended for Long-term Treatment 2. 3. E2A Clinical Safety Data Management: Definitions and Standards for Expedited Reporting E2B International Conference on Harmonisation; Guidance on Data Elements for Transmission of Individual of Non-Life-Threatening Conditions Case Safety Reports (Issued 1/15/1998, Posted 1/15/1998) o E2BM Data Elements for Transmission Of Individual Case Safety Reports 4/4/2002) (Issued 4/2002, Posted 4. E2C Clinical Safety Data Management: Periodic Safety Update Reports for Marketed Drugs 5/19/1997, Posted 3/19/1998) 5. E3 Structure and Content of Clinical Study Reports 6. E4 Dose-Response Information to Support Drug Registration 7. E5 Ethnic Factors in the Acceptability of Foreign Clinical Data 8. E6 Good Clinical Practice: Consolidated Guideline (Issued (Issued 6/10/1998, Posted 6/10/1998) Spanish Version (Issued 5/9/1997, Posted 3/19/1998) 9. E7 Studies in Support of Special Populations: Geriatrics 10. E8 General Considerations for Clinical Trials (Issued 12/1997, Posted 12/17/1997) (9/1/1998) 11. E9 Statistical Principles for Clinical Trials 12. E 10 Choice of Control Group and Related Issues in Clinical Trials [HTML] or [PDF] (Issued 5/2001, Posted 5/11/2001) 13. E11 Clinical Investigation of Medicinal Products in the Pediatric Population [Acrobat] (Issued 12/2000, Posted 12/14/2000) Quality 1. 2. Q1A(R) Stability Testing of New Drug Substances and Products [HTML] or [PDF] (Posted 11/6/2001) Q1B Photostability Testing of New Drug Substances and Products [HTML] or [PDF] (Issued 11/1996, Reposted 7/7/1998) 3. 4. Q1C Stability Testing for New Dosage Forms (Issued 5/9/1997, Posted 3/19/1998) Q1D Bracketing and Matrixing Designs for Stability Testing of New Drug Substances and Products [Word] or [PDF] (Issued 1/2003, Posted 1/15/2003) 5. Q2A Text on Validation of Analytical Procedures 6. 7. Q2B Validation of Analytical Procedures: Methodology (Issued 5/19/1997, Posted 3/19/1997) Q3A Impurities in New Drug Substances [Word] or [PDF] (Issued 2/10/2003, Posted 2/10/2003) 8. Q3B Impurities in New Drug Products or Adobe Acrobat version 9. Q3C Impurities: Residual Solvents or Adobe Acrobat version (Issued 5/19/1997, Reposted 7/7/1998) (Issued 12/24/1997, Posted 12/30/1997) Q3C Tables and List or Adobe Acrobat version (Posted 10/2/2001). Appendix 4, Appendix 5, and Appendix 6 (Appendices were issued with the Q3C draft guidance documents) Maintenance Procedures for Updating (Posted 2/11/2002) 10. Q5A Viral Safety Evaluation of Biotechnology Products Derived From Cell Lines of Human or Animal Origin (Posted 9/1998) 11. Q5B Quality of Biotechnological Products: Analysis of the Expression Construct in Cells Used for Production of r-DNA Derived Protein Products 12. Q5C Quality of Biotechnological Products: Stability Testing of Biotechnological/Biological Products 13. Q5D Quality of Biotechnological/Biological Products: Derivation and Characterization of Cell Substrates Used for Production of Biotechnological/Biological Products; Availability (Issued 9/21/1998, Posted 9/21/1998) 14. Q6A International Conference on Harmonisation; Guidance on Q6A Specifications: Test Procedures and Acceptance Criteria for New Drug Substances and New Drug Products: Chemical Substances. [Text] or [PDF] (12/29/2000) 15. Q6B Specifications: Test Procedures and Acceptance Criteria for Biotechnological/Biological Products [PDF] (Issued 8/1999, Posted 12/14/2001) 16. Q7A Good Manufacturing Practice Guidance for Active Pharmaceutical Ingredients [HTML] or [PDF] (Issued 8/2001, Posted 9/24/2001] International Conference on Harmonisation (Draft) Efficacy 1. E2C Addendum to ICH E2C Clinical Safety Data Management Periodic Safety Update Reports for Marketed 2. Drugs (Issued 9/2002, Posted 12/27/2002) Principles for Clinical Evaluation of New Antihypertensive Drugs. Optional Format: PDF. (Issued 8/2000, Posted 8/8/2000) Joint Safety/Efficacy (Multidisciplinary) (Draft) 1. 2. 3. M2 Electronic Common Technical Document Specification [HTML] or [PDF] (Issued 6/2002, Posted 6/13/2002) Submitting Marketing Applications According to the ICH/CTD Format: General Considerations (Issued 9/2001, Posted 9/5/2001) [PDF] M4 Common Technical Document--Quality: Questions and Answers/Location Issues [HTML] or [PDF] or [WORD] (Issued 9/12/2002, Posted 12/30/2002) Quality 1. 2. 3. Q3B(R) Impurities in New Drug Products [Text] or [PDF] (Issued 7/2000, Posted 7/19/2000) Q1E Evaluation of Stability Data [HTML] or [PDF] (Issued 6/2002, Posted 6/13/2002) Q1F Stability Data Package for Registration in Climatic Zones III and IV [HTML] or [PDF] (Issued 6/2002, Posted 6/13/2002) Safety 1. S7B Safety Pharmacology Studies for Assessing the Potential for Delayed Ventricular Repolarization (QT Interval Prolongation) by Human Pharmaceuticals [HTML] or [PDF] (Issued 6/2002, Posted 6/13/2002) Investigational New Drug Applications 1. Content and Format of Investigational New Drug Applications (INDs) for Phase 1 Studies of Drugs Labeling The unlinked guidance's below have been withdrawn. See Federal Register Notice from July 5, 2002 : [Text] or [PDF] 1. 2. 3. 4. 5. 6. 7. 8. 9. 10. 11. 12. 13. 14. 15. 16. 17. 18. 19. 20. 21. 22. 23. 24. 25. 26. 27. 28. 29. 30. 31. 32. 33. 34. 35. 36. 37. 38. 39. 40. 41. 42. 43. 44. 45. 46. 47. Acetaminophen, Aspirin and Codeine Phosphate Tablets and Acetaminophen, Aspirin and Codeine Phosphate Capsules Acetaminophen and codeine Phosphate Oral Solution and oral suspension (Issued 12/1993, Posted 7/11/1997) Alprazolam Tablets or WordPerfect 6.x Version (Issued 8/1996, Posted 8/21/1997) Amiloride Hydrochloride and Hydrochlorothiazide Tablets USP (Issued 9/1997, Posted 10/16/1997) Amlodipine Besylate Tablets (Issued 9/1997, Posted 10/15/1997) Astemizole Tablets (Issued 9/1997, Posted 10/15/1997) Atenolol Tablets or WordPerfect 6.x Version (Issued 8/1997, Posted 8/21/1997) Butalbital, Acetaminophen and Caffeine Tablets USP, Butalbital, Acetaminophen and Caffeine Capsules USP (Issued 9/1997, Posted 10/16/1997) Butalbital, Acetaminophen, Caffeine and Hydrocodone Bitartrate Tablets (Issued 9/1997, Posted 10/16/1997) Butorphanol Tartrate Injection USP Captopril and Hydrochlorothiazide Tablets, USP Captopril Tablets (Issued 2/1995, Posted 7/11/1997) Carbidopa and Levodopa Tablets USP Cimetidine Hydrochloride Injection (Issued 9/1995, Posted 7/11/1997) Cimetidine Tablets, USP Cisapride Oral Suspension (Issued 9/1997, Posted 10/16/1997) Cisapride Tablets (Issued 9/1997, Posted 10/20/1997) Clindamycin Phosphate Injection USP (Revised 9/1998, Posted 10/15/1998) Content and Format for Geriatric Labeling [HTML] or [PDF] (Issued 10/2001, Posted 10/4/2001) Diclofenac Sodium Delayed-release Tablets Diltiazem Hydrochloride Extended-release Capsules Diphenoxylate Hydrochloride and Atropine Sulfate Oral Solution, USP Diphenoxylate Hydrochloride and Atropine Sulfate Tablets, USP Fludeoxyglucose F18 Injection (Issued 1/1997, Posted 3/1/1997) Flurbiprofen Tablets USP Fluvoxamine Maleate Tablets (Issued 9/1997, Posted 10/20/1997) Gentamicin Sulfate Ophthalmic Solution USP and Gentamicin Sulfate Ophthalmic Ointment USP Heparin Sodium Injection, USP Hydrocodone Bitartrate and Acetaminophen Tablets USP Indomethacin Capsules, USP Itraconazole Capsules (Isssued 9/1998, Posted 10/15/1998) Leucovorin Calcium for Injection (Issued 7/1996, Posted 7/11/1997) Leucovorin Calcium Tablets USP (Issued 7/1996, Posted 7/11/1996) Medroxyprogesterone Acetate Tablets, USP (Revised 9/1998, Posted 10/15/1998) Metaproternol Sulfate Inhalation Solution USP Metaproterenol Sulfate Syrup, USP Metaproterenol Sulfate Tablets, USP Metoclopramide Tablets USP and Metoclopramide Oral Solution USP Naproxen Sodium Tablets USP (Issued 9/1997, Posted 10/16/1997) Naproxen Tablets USP (Issued 9/1997, Posted 10/16/1997) Paclitaxel Injection (Issued 9/1997, Posted 10/15/1997) Quinidine Sulfate Tablets USP (Issued 10/1995, Posted 7/11/1997) Ranitidine Tablets USP Risperidone Oral Solution (Issued 9/1997, Posted 10/15/1997) Risperidone Tablets (Issued 9/1997, Posted 10/15/1997) Sulfacetamide Sodium Ophthalmic Solution USP and Sulfacetamide Sodium Ophthalmic Ointment USP Sulfacetamide Sodium and Prednisolone Acetate 48. Sulfamethoxazole and Trimethoprim Tablets USP and Sulfamethoxazole and Trimethoprim Oral Suspension USP 49. Theophylline 50. Theophylline Intravenous Dosage Forms (Issued 9/1/1995, Posted 7/11/1997) 51. Tobramycin Sulfate Injection USP 52. Venlafaxine Hydrochloride Tablets (Issued 10/1997, Posted 12/23/1997) 53. Verapamil Hydrochloride Tablets 54. Zolpidem Tartrate Tablets (Issued 9/1997, Posted 10/15/1997) Labeling (Draft) 1. 2. 3. 4. 5. 6. Clinical Studies Section of Labeling for Prescription Drugs and Biologics-- Content and Format [HTML] or [PDF] (Issued 7/2001, Posted 7/9/2001) Combined Oral Contraceptives - Labeling for Healthcare Providers and Patients [HTML] or [PDF] (Issued 7/2000, Posted 7/7/2000) Content and Format of the Adverse Reactions Section of Labeling for Human Prescription Drugs and Biologics [HTML] or [PDF] (Issued 6/2000, Posted 6/20/2000) Draft Guidance for Industry on Labeling of OTC Topical Drug Products for the Treatment of Vaginal Yeast Infections (Vulvovaginal Candidiasis) (Issued 6/1998, Posted 7/20/98) Labeling Guidance for Noncontraceptive Estrogen Drug Products for the Treatment of Vasomotor Symptoms and Vulvar and Vaginal Atrophy Symptoms — Prescribing Information for Health Care Providers and Patient Labeling [Word] or [PDF] (Posted 1/31/2003) Referencing Discontinued Labeling for Listed Drugs in Abbreviated New Drug Applications [HTML] or [PDF] (Issued 10/2000, Posted 10/25/2000) Microbiology 1. Format and Content of the Microbiology Section of an Application* Modernization Act of 1997 1. Changes to an Approved NDA or ANDA [HTML] or [PDF] (Issued 11/1999, Posted 11/19/1999) 2. Classifying Resubmissions in Response to Action Letters 3. Enforcement Policy During Implementation of Section 503A of the Federal Food, Drug, and Cosmetic Act Word Version (Issued 11/1998, Posted 11/20/1998) 4. Fast Track Drug Development Programs – Designation, Development, and Application Review 5. 6. 7. 8. 9. (Issued 5/14/1998, Posted 5/14/1998) or ; Appendix 3 consisting of Mapp 6020.3 and SOPP 8405;and Appendix 4 [Appendices are Appendix 2 scanned copies, which will be replaced by final versions 11/18] (Issued 11/17/1998, Posted 11/17/1998) Formal Dispute Resolution: Appeals Above the Division Level [HTML] or [PDF] (Issued 2/2000, Posted 3/6/2000) Formal Meetings With Sponsors and Applicants for PDUFA Products [HTML] or [PDF] (Issued 2/2000, Posted 3/6/2000) Implementation of Section 120 of the Food and Drug Administration Modernization Act of 1997-Advisory Committees Wordperfect or Acrobat Version (Issued 10/1998, Posted 11/02/98) Implementation of Section 126 of the Food and Drug Administration Modernization Act of 1997 - Elimination of Certain Labeling Requirements (Issued 7/1998, Posted 7/20/98) Information Program on Clinical Trials for Serious or Life-Threatening Diseases and Conditions [HTML] or [PDF] (Issued 3/2002, Posted 3/18/2002) 10. National Uniformity for Nonpresciption Drugs - Ingredient Listing for OTC Drugs 5/5/1998) (Issued 4/1998, Posted (Issued 5/14/1998, 11. Providing Clinical Evidence of Effectiveness for Human Drug and Biological Products Posted 5/14/1998) 12. Qualifying for Pediatric Exclusivity Under Section 505A of the Federal Food, Drug, and Cosmetic Act [HTML] or [PDF] (Issued 9/1999, Posted 10/4/1999) o Frequently Asked Questions on Pediatric Exclusivity (505A), The Pediatric "Rule," and Their Interaction (Posted 7/27/1999) 13. Repeal of Section 507 of the Federal Food, Drug and Cosmetic Act (Revised 5/1998, Posted 6/12/1998) 14. Standards for Prompt Review of Efficacy Supplements (Issued 5/15/1998, Posted 5/15/1998) 15. Submission of Abbreviated Reports and Synopses in Support of Marketing Applications (Issued 8/1998, Posted 9/15/98) 16. Submitting and Reviewing Complete Responses to Clinical Holds (Revised) [HTML] or [PDF] (Issued 10/2000, Posted 10/25/2000 17. Women and Minorities Guidance Requirements (Issued 7/20/1998, Posted 11/25/1998) Modernization Act of 1997 (Draft) 1. 2. 3. Information Program on Clinical Trials for Serious or Life-Threatening Diseases: Establishment of a Data Bank [HTML] or PDF (Issued 3/2000, Posted 3/28/2000) PET Drug Applications - Content and Format for NDAs and ANDAs [HTML] or [PDF] (Issued 3/7/2000, Posted 3/7/2000) o Sample formats for chemistry, manufacturing, and controls sections [PDF] or [Word97] o Sample formats for labeling [PDF] or [Word97] o Sample formats for Form FDA 356h [PDF] or [Word97] o Sample formats for user fee Form FDA 3397 [PDF] or [Word97] Reports on the Status of Postmarketing Studies - Implementation of Section 130 of the Food and Drug Administration Modernization Act of 1997 [HTML] or [PDF] (Posted 4/4/2001) Over-the-Counter (OTC) Guidances 1. Enforcement Policy on Marketing OTC Combination Products (CPG 7132b.16) 2. 3. (Posted 3/2/1998) General Guidelines for OTC Combination Products Labeling OTC Human Drug Products Using a Column Format [HTML] or [PDF] (Issued 12/2000, Posted 12/18/2000) Labeling OTC Human Drug Products Updating Labeling in RLDs and ANDAs [Word] or [PDF] Example Drug Facts Labels o Acetaminophen 120 mg in a Suppository Dosage Form [PDF] o Acetaminophen 325 mg in a Suppository Dosage Form [PDF] o Acetaminophen 650 mg in a Suppository Dosage Form [PDF] o Cimetidine 200 mg in a Tablet Dosage Form [PDF] o Clemastine Fumerate 1.34 mg in a Tablet Dosage Form [PDF] o Doxylamine Succinate 25 mg Tablet Dosage Form [PDF] o Ibuprofen 200 mg in a Tablet/Capsule Dosage Form [PDF] o Loperamide HCl in a Liquid Dosage Form [PDF] o Loperamide HCl in a Tablet/Caplet Dosage Form [PDF] o Miconazole Nitrate Vaginal Products [PDF] o Minoxidil Topical Solution 2% for Men and Women [PDF] o Minoxidil Topical Solution 5% for Men [PDF] o Naproxen Sodium 220 mg in a Tablet/Caplet/Gelcap Dosage Form [PDF] o Pseudoephedrine HCl Extended-Release Tablets 120 mg [PDF] 4. 5. Upgrading Category III Antiperspirants to Category I (43 FR 46728-46731) (Posted 3/2/1998) (Posted 3/2/1998) Over-the-Counter (OTC) Draft 1. 2. Labeling OTC Human Drug Products -Submitting Requests for Exemptions and Deferrals [HTML] or [PDF] (Issued 12/2000, Posted 12/18/2000) Labeling OTC Human Drug Products Updating Labeling in ANDAs [HTML] or [PDF] (2/21/2001) o o o Additional examples 1 (3/19/2001) Additional examples 2 (3/26/2001) Additional examples 3 (3/26/2001) Pharmacology/Toxicology 1. 2. Carcinogenicity Study Protocol Submissions [HTML] or [PDF] (Issued 5/22/2002) Content and Format of INDs for Phase 1 Studies of Drugs, Including Well-Characterized, Therapeutic, Biotechnology-Derived Products [HTML] or [PDF] 3. Format and Content of the Nonclinical Pharmacology/Toxicology Section of an Application* (Posted 3/2/1998) Immunotoxicology Evaluation of Investigational New Drugs [Word] or [PDF] (Issued 10/2002, Posted 10/31/2002) 4. 5. 6. Nonclinical Pharmacology/Toxicology Development of Topical Drugs Intended to Prevent the Transmission of Sexually Transmitted Diseases (STD) and/or for the Development of Drugs Intended to Act as Vaginal Contraceptives Reference Guide for the Nonclinical Toxicity Studies of Antivial Drugs Indicated for the Treatment of N/A Non- 7. Single Dose Acute Toxicity Testing for Pharmaceuticals Life Threatening Disease Evaluation of Drug Toxicity Prior to Phase I Clinical Studies (Posted 3/2/1998) Pharmacology/Toxicology Draft 1. 2. 3. 4. 5. 6. Estimating the Safe Starting Dose in Clinical Trials for Therapeutics in Adult Healthy Volunteers [Word] or [PDF] (Issued 1/2003, Posted 1/15/2003) Integration of Study Results to Assess Concerns about Human Reproductive and Developmental Toxicities [PDF] (Issued 11/2001, Posted 11/9/2001) Nonclinical Safety Evaluation of Pediatric Drug Products [Word] or [PDF] (Issued 1/2003, Posted 1/31/2003) Nonclinical Studies for Development of Pharmaceutical Excipients [Word] or [PDF] (Issued 10/2002, Posted 10/2/2002) Photosafety Testing [HTML] or [PDF] (Issued 1/2000, Posted 1/7/2000) Statistical Aspects of the Design, Analysis, and Interpretation of Chronic Rodent Carcinogenicity Studies of Pharmaceuticals [HTML] or [PDF] (Issued 5/2001, Posted 5/7/2001) Procedural 1. 2. 3. 180-Day Generic Drug Exclusivity Under the Hatch-Waxman Amendments to the Federal Food, Drug, and Cosmetic Act (Issued 6/1998, Posted 6/22/1998) Court Decisions, ANDA Approvals, and 180-Day Exclusivity Under the Hatch-Waxman Amendments to the Federal Food, Drug, and Cosmetic Act [HTML] or [PDF] (Posted 3/27/2000) Disclosure of Materials Provided to Advisory Committees in Connection with Open Advisory Committee Meetings Convened by the Center for Drug Evaluation and Research Beginning on January 1, 2000 [HTML] or [PDF] (Issued 11/1999, Posted 11/29/1999) 4. Enforcement Policy During Implementation of Section 503A of the Federal Food, Drug, and Cosmetic Act Word Version (Issued 11/1998, Posted 11/20/1998) 5. Fast Track Drug Development Programs – Designation, Development, and Application Review or Appendix 2 ; Appendix 3 consisting of Mapp 6020.3 and SOPP 8405;and Appendix 4 [Appendices are scanned copies, which will be replaced by final versions 11/18] (Issued 11/17/1998, Posted 11/17/1998) 6. Financial Disclosure by Clinical Investigators (3/27/2001) 7. Formal Dispute Resolution: Appeals Above the Division Level [HTML] or [PDF] (Issued 2/2000, Posted 3/6/2000) 8. Formal Meetings With Sponsors and Applicants for PDUFA Products [HTML] or [PDF] (Issued 2/2000, Posted 3/6/2000) 9. Implementation of Section 120 of the Food and Drug Administration Modernization Act of 1997-Advisory Committees Wordperfect or Acrobat Version (Issued 10/1998, Posted 11/02/98) 10. Implementation of Section 126 of the Food and Drug Administration Modernization Act of 1997 - Elimination of Certain Labeling Requirements (Issued 7/1998, Posted 7/20/98) 11. Information Program on Clinical Trials for Serious or Life-Threatening Diseases and Conditions [HTML] or [PDF] (Issued 3/2002, Posted 3/18/2002) 12. Information Request and Discipline Review Letters Under the Prescription Drug User Fee Act [HTML] or [PDF] (Issued 11/2001) 13. Levothyroxine Sodium Products Enforcement of August 14, 2001 Compliance Date and Submission of New Applications [HTML] or [PDF] (Issued 7/2001, Posted 7/12/2001) 14. National Uniformity for Nonpresciption Drugs - Ingredient Listing for OTC Drugs (Issued 4/1998, Posted 5/5/1998) 15. Potassium Iodide as a Thyroid Blocking Agent in Radiation Emergencies [HTML] or [PDF] (Issued 12/2001, Posted 12/10/2001) o KI in Radiation Emergencies-Questions and Answers [HTML] or [PDF] (Issued 12/20/2002, Posted 12/23/2002) 16. Reduction of Civil Money Penalties for Small Entities (Issued 3/20/2001) 17. Qualifying for Pediatric Exclusivity Under Section 505A of the Federal Food, Drug, and Cosmetic Act [HTML] or [PDF] (Issued 9/1999, Posted 10/4/1999) 18. Refusal to File (Issued 7/12/1993, Posted 11/26/99) 19. Repeal of Section 507 of the Federal Food, Drug and Cosmetic Act (Revised 5/1998, Posted 6/12/1998) 20. Special Protocol Assessment [HTML] or [PDF] (Issued 5/2002, Posted 5/16/2002) 21. Standards for Prompt Review of Efficacy Supplements (Issued 5/15/1998, Posted 5/15/1998) Procedural Draft 1. 2. 3. 4. 5. 6. 7. Applications Covered by Section 505(b)(2) [HTML] or [PDF] or [Word] (Issued 10/1999, Posted 12/7/1999) Collection of Race and Ethnicity Data in Clinical Trials [Word] or [PDF] (Issued 1/2003, Posted 1/23/2003) Disclosing Information Provided to Advisory Committees in Connection with Open Advisory Committee Meetings Related to the Testing or Approval of New Drugs and Convened by the Center for Drug Evaluation and Research, Beginning on January 1, 2000 [HTML] or [PDF] (Issued 12/1999, Posted 12/22/1999) Disclosure of Conflicts of Interest for Special Government Employees Participating in FDA Product Specific Advisory Committees [HTML}or [PDF] (2/14/2002) Forms for Registration of Producers of Drugs and Listing of Drugs in Commercial Distribution [HTML] or [PDF] (5/14/2001) Guidance for Federal Agencies and State and Local Governments Potassium Iodide Tablets Shelf Life Extension [HTML] - [Word] - [PDF] (Posted 4/1/2003) PET Drug Applications - Content and Format for NDAs and ANDAs (Issued 3/7/2000, Posted 3/7/2000) o o o o 8. 9. Sample formats for chemistry, manufacturing, and controls sections Sample formats for labeling Sample formats for Form FDA 356h Sample formats for user fee Form FDA 3397 (Issued 3/2001, Postmarketing Safety Reporting for Human Drug and Biological Products Including Vaccines Posted 3/9/2001) Reports on the Status of Postmarketing Studies - Implementation of Section 130 of the Food and Drug Administration Modernization Act of 1997 [HTML] or [PDF] (Posted 4/4/2001) 10. Submitting Debarment Certification Statements (Issued 10/2/98, Posted 10/2/98) 11. Submitting Marketing Applications According to the ICH/CTD Format: General Considerations [PDF] (Issued 9/2001, Posted 9/5/2001) 12. The Use of Clinical Holds Following Clinical Investigator Misconduct (Issued 4/2002, Posted 8/26/2002) Small Entity Compliance Guides 1. Sterility Requirement for Aqueous-Based Drug Products for Oral Inhalation — Small Entity Compliance Guide [PDF] (Posted 11/7/2001) User Fees 1. 2. 3. 4. Classifying Resubmissions in Response to Action Letters (Issued 5/14/1998, Posted 5/14/1998) Fees-Exceed-the-Costs Waivers Under the Prescription Drug User Fee Act [HTML] or [PDF] (Issued 6/1999, Posted 6/25/99) Information Request and Discipline Review Letters Under the Prescription Drug User Fee Act [HTML] or [PDF] (Issued 11/2001) Submitting and Reviewing Complete Responses to Clinical Holds (Revised) [HTML] or [PDF] (Issued 10/2000, Posted 10/25/2000) User Fees (Draft) 1. Submitting Separate Marketing Applications and Clinical Data for Purposes of Assessing User Fees [PDF] (2/21/2001) Also see Current Good Manufacturing Practice Regulations Enforcement of the Postmarketing Adverse Drug Experience Reporting Regulations (Posted 8/11/1997) [Accessibility] CDER Home Page | Search | Comment | What's New 12/17/2001 MEMBERGROUPS Approx Statistician Members Country Group Belgium SBS/BVS (Société Belge de Statistique / Belgische Verenining voor Statistiek - Biostatistics section)........... .82 Denmark DSBS (Dansk Selskab for Biofarmaceutisk Statistik)........... .68 Finland SSL (Statistikot Suomen lääketeollisuudessa) .47 France SFdS (Société Francaise de Statistique - Biopharmacy and Health Group)........... .168 APF (Arbeitsgruppe Pharmazeutische Forschung of German region of International Biometric Society)........... .272 Germany Italy BIAS (Biometristi dell'industria Farmaceutica Associati)..... .75 Netherlands PSDM (werkgreop Pharmaceutische Statistiek en Datamanagement van Verenining voor Statistiek - Biometrische Sectie)........... .80 ABCif (Asociación de Biometria Clinica para la Investigacion Farmaceutica)........... .40 Spain Sweden FMS (Föreningen för Medicinsk Statistik)........... Switserland BBS (Basler Biometrische Sektion) of International Biometric Society........... United Kingdom Total................ PSI (Statisticians in the Pharmaceutical Industry)........... .105 .75 .1060 .2072 GENERAL INFORMATION EFSPI, the European Federation of Statisticians in the Pharmaceutical Industry, is open to constituted groups of statisticians. Eligibility for membership is open to one national group per country placing a major emphasis on technical and scientific activities directed at statisticians who are working in or for the pharmaceutical industry. Thus, EFSPI is engaged in statistical aspects of research, development, production, and surveillance of drugs and medical devices. The constitutional objectives of the Federation are: To promote professional standards of statistics and the standing of the statistical profession in matters pertinent to the European pharmaceutical industry. To offer a collective expert input on statistical matters to national and international authorities and organisations. To exchange information on and harmonise attitudes to the practice of statistics in the European pharmaceutical industry and within the member groups. After constitutional meetings since 1990, the Federation was officially launched in August 1992. There are now 11 member groups including over 2000 pharmaceutical statisticians in Europe. ACHIEVEMENTS (related to objectives of EFSPI) To promote professional standards of statistics and the standing of the statistical profession in matters pertinent to the European pharmaceutical industry: EFSPI Working Party published report and paper on the qualifications and experience needed to be a professional statistician in the pharmaceutical industry. Published in Drug Information Journal, vol 33 (2), 1999. Presented at conferences of International Statistical Institute (Helsinki, 1999), Royal Statistical Society (Reading, 2000), PSI (Southampton, 1999), FMS (Umeå, Sweden, 1999), Italian Statistical Society (Bressanone, Italy, 2000). EFSPI set up clinical statistics meetings with DIA in London (1993), Edinburgh (1994), Nice (1997) and Brussels (1999). EFSPI was engaged in non-clinical statistics meetings with DIA in Bruges (1996), Nice (1998), Montreux (2000). EFSPI organised invited sessions at the International Statistical Institute conference in Florence (1993) and Helsinki (1999). ٧ To offer a collective expert input on statistical matters to national and international authorities and organisations: Joint EFSPI/EFPIA working party provided European input on consultation drafts of ICH E9 (1997) and E10 (1999). EFSPI co-ordinated input from national member groups to provide single European pharmaceutical statistics view on ICH and CPMP consultation documents. EFSPI was asked specifically for input by CPMP on Points to Consider document on Meta Analysis and One Single Study. EFSPI published a critical review of ICH E10 in Drug Information Journal, vol 35 (4), 2001. To exchange information on and harmonise attitudes to the practice of statistics in the European Pharmaceutical Industry and within member groups EFSPI web-site contains links to all member groups web-sites. There is a free exchange of information between Federation member groups in the areas of meetings, courses, conferences, working parties, expert teams and ad hoc groups. Activities organised by member groups are open to individual members of any Federation member group. EFSPI exchanges information with corresponding US and Japanese groups. Informal networks established to facilitate communication between statisticians working in the non-clinical and veterinary areas. EFSPI (European Federation of Statisticians in the Pharmaceutical Industry) • There is a working party for commenting the guidelines on statistical issues produced by ICH, EMEA, FDA • For every concerned guideline, a person responsible for collecting the comments from the national organisations is appointed. This person is responsible for collating all the comments received from his/her organisation and solving the conflicting ones, when possible PROCESS FOR RE VIE WING DOCUMENTS FOR EFSPI 1. Contact person chosen at EFSPI meeting for all upcoming regulatory documents to be reviewed. 2. Regulatory document sent by the regulatory affairs chairman to the appropriate EFSPI contact person. 3. EFSPI contact person sends a mail as soon as possible to all National contacts requesting that they organise and collate the comments from their national organization on the document using the standard form (reply form). The contact person should receive their comments at the latest one month before comments are due. 4. Each country contact collects the comments from his/her member group, or delegates someone else to do so. This can be done by a formal meeting, luncheon meeting, regulatory affairs sub-committee, etc. 5. Before sending these comments to the EFSPI contact person, the country contact should discern major comments from minor comments, and also separate any typing errors (see reply form). Contradicting comments from within the national organisation should be avoided, or clearly identified as such in the reply. 6. In case of many comments, the national contact may want to circulate the collated version to his or her national group for approval before sending to the EFSPI contact person. 7. The EFSPI contact person then collates all country comments into one form again avoiding contradicting comments where possible, and sends it to all national contacts. Usually only one week is available for replies so the national contacts have to be aware of this. 8. The final document is then sent to the regulatory affairs chairman who forwards it to the appropriate place. Copies of the final document are also sent to all EFSPI council members who can then send them back to their national organisations if requested. Draft 1 — 10 October 2002 page 1 of 1 Armonizzazione del comportamento dei biostatistici nel contesto decisionale dei Comitati etici prof. Marubini dr.ssa Patarnello Armonizzazione dei comportamenti dei biostatistici nel contesto decisionale dei Comitati Etici F. Patarnello, E. Marubini Giornata su "Le competenze biostatistiche nell'ambito dei Comitati etici locali", Roma 18 marzo 2003 1 Quale e’ la situazione? ...dalla parte dello Sponsor (da indagine) • poco frequenti contatti diretti tra biostatistico CE e Sponsor, e spesso senza qualificare da chi origina il quesito • poco frequenti quesiti sul disegno sperimentale, tranne per il gruppo di controllo, in particolare sul placebo, qualcuno su sample size, qualcuno su analisi statistica. Frequentemente dopo chiarimento i punti non vengono modificati. Prevalgono aspetti amministrativi, assicurativi, sul consenso informato. • possibili i casi di valutazioni diverse su protocolli simili in tempi diversi o in CE diversi • rarissime le richieste di risultati degli studi o sui risultati • nessun caso di valutazioni preliminari del disegno dello studio tra CE e Sponsor (tipo FDA) Giornata su "Le competenze biostatistiche nell'ambito dei Comitati etici locali", Roma 18 marzo 2003 2 Quale e’ la situazione? ...dalla parte del CE (autocritica) • Protocolli internazionali preconfezionati e non modificabili • Alcuni studi non correttamente dimensionati (studi pilota?) • Studi simili negli obiettivi ma con metodologia diversa e sample size diversi • Analisi statistica o non sufficientemente descritta o troppo complessa, ma scarsamente riproducibile • Scarsa attenzione alla diffusione e discussione dei risultati e al controllo dell’effettiva analisi rispetto a quella pianificata Giornata su "Le competenze biostatistiche nell'ambito dei Comitati etici locali", Roma 18 marzo 2003 3 Armonizzazione: cosa non significa? • replicare sempre lo stesso disegno e la stessa analisi (ogni studio e’ diverso) • seguire le linee guida in modo burocratico • seguire la letteratura in modo acritico • comportarsi allo stesso modo in aree terapeutiche e in fasi di sviluppo del farmaco diverse Giornata su "Le competenze biostatistiche nell'ambito dei Comitati etici locali", Roma 18 marzo 2003 4 • Armonizzazione: cosa significa? agire con coerenza nei confronti del problema e dell’obiettivo dello studio • costruire, studiare, capire, e applicare le linee guida non rinunciando mai alla discussione di casi specifici o eccezionali • essere informati sulle specificita’ metodologiche presenti letteratura e non ragionare per ogni studio come se fosse il primo • specializzarsi in varie aree terapeutiche e in fasi di sviluppo del farmaco diverse • utilizzare la stessa accuratezza nella valutazione metodologica indipendentemente dallo sponsor, dal disegno sperimentale (caso degli studi osservazionali), dalla fase, dal tipo di trattamento (farmaco, device, chirurgia) ma basandosi sull’obiettivo Giornata su "Le competenze biostatistiche nell'ambito dei Comitati etici locali", Roma 18 marzo 2003 5 Strumenti • Formazione e aggiornamento comune • Costruire le regole insieme • Dialogo diretto tra biostatistici nei CE e presso lo sponsor • Trasparenza e disponibilita’ delle valutazioni • Discussioni preliminari sui protocolli • Attenzione ai risultati • Controlli di qualita’ : rilevazione continua delle differenze (dummy protocol?) Giornata su "Le competenze biostatistiche nell'ambito dei Comitati etici locali", Roma 18 marzo 2003 6 Organizzazione dello scambio informatizzato di commenti e pareri prof. Grigoletto dr.ssa Rinieri Organizzazione dello scambio informatizzato di commenti e pareri La funzione dell’Osservatorio Roma, 18 marzo 2003 Elisa Rinieri Obiettivi 1 Il sistema è progettato per essere un registro delle sperimentazioni cliniche sui farmaci condotte in Italia che raccoglie tutte le informazioni relative ad approvazione, avvio e conclusione, incluse le informazioni relative alle reazioni avverse Obiettivi 2 Creare una rete per facilitare la comunicazione dei dati e lo scambio di informazioni tra tutti i partecipanti alla sperimentazione (Comitati Etici dei centri partecipanti, Sponsor, autorità competenti, Ministero della Salute) Scambio di informazioni: rete e sottoreti di comunicazione Rete tra tutti i Comitati Etici e tutti gli Sponsor Per ogni studio creazione di una sottorete per gli Sponsor ed i Comitati Etici coinvolti Obiettivi 3 • Monitorare l’intero processo della sperimentazione clinica e produrre statistiche al fine di fornire al Ministero della Salute una visione globale delle sperimentazioni cliniche condotte in Italia • Produrre un Rapporto Nazionale Annuale delle sperimentazioni cliniche in Italia Il sistema L’Osservatorio Nazionale sulla Sperimentazione Clinica è basato sulla metodologia AMR - Advanced Multicenter Research completamente web-based E’ accessibile in Internet attraverso un browser standard (Microsoft Internet Explorer, Netscape Communicator). Powered by Web technology Approvazione delle sperimentazioni in Italia Fase II, III RICHIESTA Sponsor Rilascio del GdN dal Comitato Etico del Centro Coordinatore o Ministero della Salute (Ufficio Sperimentazione Clinica) Parere favorevole dell’Istituto Superiore di Sanità sulla sicurezza e qualità del medicinale SI RICHIESTA Fase IV Sponsor RICHIESTA Sponsor Fase I SI Richiesta di approvazione della sperimentazione ai Comitati Etici dei Centri partecipanti NO SI SI SI SI INIZIO DELLO STUDIO Inserimento elettronico dei dati Per ogni sperimentazione clinica lo sponsor inserisce i dati richiesti direttamente attraverso form elettroniche via web In seguito al ricevimento della form elettronica completata dallo sponsor, il Comitato Etico o l’autorità competente dovrà validare e fornire l’autorizzazione alla conduzione della sperimentazione clinica Dopo l’inserimento, gli utenti non hanno più accesso alla modifica dei dati, ogni ulteriore modifica deve essere fatta dal Ministero della Salute Accesso ai dati Ogni utente, per essere autorizzato, deve essere registrato tramite l’inserimento di alcune informazioni identificative nella scheda di registrazione accessibile via web L’ufficio competente presso il Ministero della Salute “valida” le informazioni e fornisce all’utente userid e password Profili utente L’accesso al database prevede diversi profili utente: • Sponsor/CRO • Comitati Etici • Regioni e Province Autonome • ASL • Data Review Committees • Ufficio Sperimentazione Clinica (Ministero della Salute) • Istituto Superiore di Sanità Profili di accesso • Ogni utente può accedere solo ai propri dati • Solo il Ministero della Salute – Ufficio Sperimentazione Clinica è autorizzato a vedere tutto il Registro (Controllo Centrale) • Solo gli sponsor ed i Comitati Etici sono autorizzati all’inserimento dei dati Raccolta delle informazioni 1 Per ogni studio, informazioni generali, per esempio: • Titolo del Protocollo, codice, file ed emendamenti • Sponsor e centri partecipanti • Coordinatore dello studio • Disegno dello studio (randomizzazione, nazionale, internazionale, fase…) • Codice di patologia (ICD), area terapeutica • Durata e numero di pazienti previsti nello studio • Informazioni sui farmaci (nome, dosaggio e durata del trattamento, …) • Eleggibilità (criteri di inclusione ed esclusione) • Popolazione in studio (età, sesso, …) Raccolta delle informazioni 2 Per ogni studio, dati amministrativi del flusso di approvazione e stato corrente dello studio per ogni centro coinvolto, per esempio: • Dati di approvazione dello studio • Data di apertura dello studio alla registrazione dei pazienti • Dati sullo stato corrente dello studio • Raccolta dei pazienti • Dati sulle reazioni avverse • Pubblicazioni OsSC - Database Globale Registro Registro Registro GdN CRO Sponsor Registro CT Registro Comitati Etici Registro Registro P.I. Ospedali/Reparti MMG/PLS Procedure di qualità dei dati • Filtri durante l’inserimento • Dizionari standard per minimizzare l’uso di testo libero • Controlli automatici sulla consistenza dei dati • Warning automatici • Produzione di report predefiniti sulla qualità dei dati (accuratezza, completezza, integrità) Analisi dei dati Il database è dotato di alcune funzioni di ricerca che permettono l’individuazione di informazioni specifiche attraverso parole chiave Tools di data warehouse per analisi strategiche Produzione automatica, in formato stampabile, del Rapporto Nazionale Sicurezza delle informazioni Il sistema garantisce: backup regolare su dispositivi elettronici di tutte le informazioni, per permettere il ripristino in caso di perdita o danneggiamento del database tracking log (registrazione di ogni operazione eseguita da ciascun utente) audit trials (creazione di una banca dati storica di ogni modifica effettuata con memorizzazione della data e dell’utente) Gli strumenti per lo scambio di informazioni Gli strumenti messi a disposizione dei Comitati Etici per creare una rete per facilitare la comunicazione dei dati e lo scambio di informazioni tra tutti i partecipanti alla sperimentazione Gli strumenti per lo scambio di informazioni Bacheca Condivisione dei pareri sulle sperimentazioni Comunicazione per gruppi di utenti che partecipano alla stessa sperimentazione Area contatti: comunicazioni ai Comitati Etici Area contatti: forum fra tutti gli utenti dell’OsSC Progress report Sistema di messaggistica automatica Forum con accesso riservato a gruppi particolari di utenti: p.e. ai Comitati Etici con un componente biostatistico Bacheca 1 Ogni Comitato Etico ha a disposizione uno spazio, accessibile a tutti gli utenti dell’Osservatorio in cui pubblicare comunicazioni e documenti. La bacheca deve essere utilizzata per: elenco documentazione da presentare al fine dell'ottenimento dell'autorizzazione degli studi clinici; calendario riunioni con ordine del giorno e data di scadenza per la presentazione di documenti; regolamento del Comitato Etico; eventuale indirizzo del sito Web del Comitato Etico o dell'Azienda; segnalazione di convegni, congressi, giornate di studio e seminari inerenti l'argomento. Bacheca 2 Condivisione di pareri sulle sperimentazioni 1 Ogni Comitato Etico (limitatamente alle sperimentazioni a cui partecipa) ha accesso alle informazioni relative allo stato di approvazione della sperimentazione in ciascuno degli altri Comitati Etici partecipanti Condivisione di pareri sulle sperimentazioni 2 Condivisione di pareri sulle sperimentazioni 3 Condivisione di pareri sulle sperimentazioni 4 Condivisione di pareri sulle sperimentazioni 5 Comunicazioni per gruppi di utenti che partecipano alla stessa sperimentazione 1 Ogni Comitato Etico (limitatamente alle sperimentazioni a cui partecipa) può accedere ad uno spazio riservato alle comunicazioni accessibili solo al gruppo di utenti (sponsor, Comitato Etico del centro coortinatore, Comitati Etici dei centri satellite) che partecipa ad una specifica sperimentazione Comunicazioni per gruppi di utenti che partecipano alla stessa sperimentazione 2 Comunicazioni per gruppi di utenti che partecipano alla stessa sperimentazione 3 Comunicazioni per gruppi di utenti che partecipano alla stessa sperimentazione 4 Comunicazioni per gruppi di utenti che partecipano alla stessa sperimentazione 5 Comunicazioni per gruppi di utenti che partecipano alla stessa sperimentazione 6 Area Contatti: comunicazioni ai Comitati Etici 1 Nell’area contatti è disponibile la lista di tutti i Comitati Etici abilitati all’utilizzo dell’Osservatorio con possibilità di inviare una e-mail ad un singolo Comitato Etico oppure a tutti i Comitati Etici Area Contatti: comunicazioni ai Comitati Etici 2 Area Contatti: comunicazioni ai Comitati Etici 3 Area Contatti: forum fra tutti gli utenti dell’Osservatorio Il Forum è uno spazio in cui inserire messaggi e quesiti di interesse per tutti gli utenti dell'Osservatorio; le risposte ai quesiti possono da uno qualsiasi degli utenti dell'Osservatorio e vengono pubblicate nel Forum 1 Area Contatti: forum fra tutti gli utenti dell’Osservatorio 2 Area Contatti: forum fra tutti gli utenti dell’Osservatorio 3 Area Contatti: forum fra tutti gli utenti dell’Osservatorio 4 Area Contatti: forum fra tutti gli utenti dell’Osservatorio 5 Progress Report 1 Ciascun Comitato Etico (limitatamente alle sperimentazioni a cui partecipa) ha accesso ad uno schema riassuntivo per il monitoraggio dello stato di avanzamento delle sperimentazioni Progress Report 2 Progress Report 3 Sistema di messaggistica automatica 1 Il sistema prevede l’invio di messaggi automatici per la segnalazione ai Comitati Etici della presenza di nuovi studi da approvare all’interno dell’Osservatorio Forum con accesso riservato a gruppi particolari di utenti 1 In funzione di specifiche esigenze è possibile creare sistemi per comunicazioni riservate a gruppi specifici di utenti. Ad esempio potrebbe essere creato un forum riservato ai Comitati Etici con un componente “biostatistico” Scambio informatizzato di informazioni: rete e sottoreti di comunicazione Sottorete di comunicazione fra biostatistici Rete tra tutti i Comitati Etici e tutti gli Sponsor Per ogni studio creazione di una sottorete per gli Sponsor ed i Comitati Etici coinvolti