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3 2 Clinical Trial Investigation Interpretation of Results “to p or not to p” Ferran Torres Hospital Clínic Barcelona / Universitat Autònoma Barcelona. EMA: Scientific Advice Working Party (SAWP) Biostatistics Working Party (BSWP).
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5 4 Today’s talk is on statistics
7 6 Statistics Considerations
8 [email protected] 7 Basic statistics Why Statistics? Samples and populations P-Value Random and sistematical errors Statistical errors Sample size Confidence Intervals Interpretation of CI: superiority, non- inferiority, equivalence
9 [email protected] 8 The role of statistics “Thus statistical methods are no substitute for common sense and objectivity. They should never aim to confuse the reader, but instead should be a major contributor to the clarity of a scientific argument.” The role of statistics. Pocock SJ. Br J Psychiat 1980; 137:188-190
10 [email protected] 9 Why Statistics? Variation!!!!
11 [email protected] 10 Variability
12 [email protected] 11 Why Statistics? Medicine is a quantitative science but not exact Not like physics or chemistry Variation characterises much of medicine Statistics is about handling and quantifying variation and uncertainty Humans differ in response to exposure to adverse effects Example: not every smoker dies of lung cancer some non-smokers die of lung cancer Humans differ in response to treatment Example: penicillin does not cure all infections Humans differ in disease symptoms Example: Sometimes cough and sometimes wheeze are presenting features for asthma
13 [email protected] 12 Why Statistics Are Necessary Statistics can tell us whether events could have happened by chance and to make decisions We need to use Statistics because of variability in our data Generalize: can what we know help to predict what will happen in new and different situations?
14 [email protected] 13 Population and Samples Target Population Population of the Study Sample
15 [email protected] 14 Extrapolation Sample Population Inferential analysis Statistical Tests Confidence Intervals Study Results “Conclusions”
16 [email protected] 15 Statistical Inference Statistical Tests=> p-value Confidence Intervals
17 [email protected] 16 Valid samples? Population Likely to occur Unlikely to occur Invalid Sample and Conclusions
18 [email protected] 17 P-value The p-value is a “tool” to answer the question: – –Could the observed results have occurred by chance*? – –Remember: Decision given the observed results in a SAMPLE Extrapolating results to POPULATION *: accounts exclusively for the random error, not bias p
19 [email protected] 18 P-value: an intuitive definition The p-value is the probability of having observed our data when the null hypothesis is true (no differences exist) Steps: 1) 1)Calculate the treatment differences in the sample (A-B) 2) 2)Assume that both treatments are equal (A=B) and then… 3) 3)…calculate the probability of obtaining a magnitude of at least the observed differences, given the assumption 2 4) 4)We conclude according the probability: a. a. p0.05: the differences could be explained by random, – –we assume that random explains the differences
20 [email protected] 19 Factors influencing statistical significance Signal Noise (background) Quantity Difference Variance (SD) Quantity of data
21 [email protected] 20 130150170 010203 0405 True Value Random vs Sistematic error Random Systematic (Bias) 130150170 01 05 02 03 04 True Value Example: Systolic Blood Pressure (mm Hg)
22 [email protected] 21 Random vs Sistematic error Sample size Random Bias
23 [email protected] 22 P-value A “statistically significant” result (p
24 [email protected] 23 P-value A “very low” p-value do NOT imply: – –Clinical relevance (NO!!!) – –Magnitude of the treatment effect (NO!!) With n or variability p Please never compare p-values!! (NO!!!)
25 [email protected] 24 RCT from a statistical point of view 1 homogeneous population2 distinct populations Randomisation Treatment B (control) Treatment A
26 [email protected] 25 RCT Sample Population
27 [email protected] 26 Statistics can never PROVE anything beyond any doubt, just beyond reasonable doubt!! … because of working with samples and random error
28 [email protected] 27 Type I & II Error & Power
29 [email protected] 28 Utilidad de Creer en la Existencia de Dios (según Pascal) H 0 : Dios No Existe H 1 : Dios Existe
30 [email protected] 29 Type I & II Error & Power Type I Error ( ) – –False positive – –Rejecting the null hypothesis when in fact it is true – –Standard: =0.05 – –In words, chance of finding statistical significance when in fact there truly was no effect Type II Error ( ) – –False negative – –Accepting the null hypothesis when in fact alternative is true – –Standard: =0.20 or 0.10 – –In words, chance of not finding statistical significance when in fact there was an effect
31 [email protected] 30 The planned number of participants is calculated on the basis of: –Expected effect of treatment(s) –Variability of the chosen endpoint –Accepted risks in conclusion ↗ effect ↘ number ↗ variability ↗ number ↗ risk ↘ number Sample Size
32 [email protected] 31 Sample Size The planned number of participants is calculated on the basis of: – –Expected effect of treatment(s) – –Variability of the chosen endpoint – –Accepted risks in conclusion ↗ effect ↘ number ↗ variability ↗ number ↗ risk ↘ number
33 [email protected] 32 Sample Size The planned number of participants is calculated on the basis of: – –Expected effect of treatment(s) – –Variability of the chosen endpoint – –Accepted risks in conclusion ↗ effect ↘ number ↗ variability ↗ number ↗ risk ↘ number
34 [email protected] 33 Interval Estimation Confidence interval Sample statistic (point estimate) Confidence limit (lower) Confidence limit (upper) “A probability that the population parameter falls somewhere within the interval”
35 [email protected] 34 95%CI Better than p-values… – –…use the data collected in the trial to give an estimate of the treatment effect size, together with a measure of how certain we are of our estimate CI is a range of values within which the “true” treatment effect is believed to be found, with a given level of confidence. – –95% CI is a range of values within which the ‘true’ treatment effect will lie 95% of the time Generally, 95% CI is calculated as – –Sample Estimate ± 1.96 x Standard Error
36 [email protected] 35 Superiority study d > 0 + effect IC95% d = 0 No differences d < 0 - effect Test betterControl better
37 [email protected] 36 0 Lower equivalence boundary Upper equivalence boundary Treatment more effective ->
38 [email protected] 37 Escalas de medición del efecto Riesgos
39 [email protected] 38 Cálculo de RR y OR RR ó OR > 1 RR ó OR =1 RR ó OR < 1 Factor de riesgo Ausencia de ‘efecto’ Factor protector
40 [email protected] 39 Cálculo de RR y OR No Expuestos Expuestos Enfermos Proporción en Expuestos: 0.50 Proporción en no Expuestos: 0.25 RR=2 Odds en Expuestos: 2/2=> 1 Odds en no Expuestos: 1/3 OR=3
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43 [email protected] 42 Seamos críticos En ocasiones las cosas no son lo que parecen
44 [email protected] 43 Seamos críticos Obtención de los resultados ¿Es adecuada la técnica estadística utilizada? T-Test ANOVA de medidas repetidas
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47 [email protected] 46 Seamos críticos Afirmaciones sin especificación de resultados Porcentajes sin el denominador Medias sin intervalo de confianza ¿Me fío del valor?
48 [email protected] 47 Seamos críticos A un paciente se le recomienda una intervención quirúrgica y pregunta por la probabilidad de sobrevivir. El cirujano le contesta que en las 30 operaciones que ha realizado, ningún paciente ha muerto. ¿Qué valores de P(morir) son compatibles con esta información, con una confianza del 95%? Otro ejemplo más
49 [email protected] 48 Seamos críticos Solución Límite superior del IC 95% para p=0 con n=30 Pr(X=0,n=30,p s ) = 0,025 La solución aproximada no sirve. Solución exacta, basada en la binomial: {0; 0,116} Incluso si la mortalidad es de un 11,6%, en 30 intervenciones no se observará ninguna muerte con Pr=0,025
50 [email protected] 49 Seamos críticos Si se disponen de datos... ... No se han de desperdiciar. Unos datos bien ‘torturados’ al final cantan. ¡¡¡ p
51 [email protected] 50... ¿Y lo del denominador? El famoso perro fantástico
52 [email protected] 51 Por que después pasa lo que pasa
53 [email protected] 52 Key statistical issues Multiplicity Subgroups: interaction & confounding Superiority and non-inferiority (and ) Adjustment by covariates Missing data Others –Interim analyses –Meta-analysis vs one pivotal study –Flexible designs
54 [email protected] 53 MULTIPLICITY
55 [email protected] 54 Torneo Roland Garros 1999 1ª Ronda Carlos Moyá vs Markus Hipfl
56 [email protected] 55 Lancet 2005; 365: 1591–95 To say it colloquially, torture the data until they speak...
57 [email protected] 56 Torturing data… –Investigators examine additional endpoints, manipulate group comparisons, do many subgroup analyses, and undertake repeated interim analyses. –Investigators should report all analytical comparisons implemented. Unfortunately, they sometimes hide the complete analysis, handicapping the reader’s understanding of the results. Lancet 2005; 365: 1591–95
58 [email protected] 57 DesignConductionResults
59 [email protected] 58 Multiplicity K independent hypothesis : H 01, H 02,..., H 0K S significant results ( p< ) Pr (S 1 | H 01 H 02 ... H 0K = H 0. ) = 1 - Pr (S=0|H 0. ) = 1- (1 - ) K
60 [email protected] 59 Same examples
61 [email protected] 60Multiplicity Bonferroni correction (simplified version) –K tests with level of signification of –Each test can be tested at the /k level Example: –5 independent tests –Global level of significance=5% –Each test shoud be tested at the 1% level 5% /5=> 1%
62 [email protected] 61 But this is the simplified version for the general public
63 [email protected] 62 Cautionary Example RCT to treat rheumatoid arthritis Basic Clin Med 1981, 15: 445 Several end ‑ points repeated at various timepoints and various subdivisions 48 of these gave p-values < 0.05 But… expect 5% of 850 = 850/20 = 42.5 =>so finding 48 is not very impressive
64 [email protected] 63 Some strategies to ‘burden’ with multiple contrasts
65 [email protected] 64 Handling Multiplicity in Variables Scenario 1:One Primary Variable –Identify one primary variable -- other variables are secondary –Trial is positive if and only if primary variable shows significant (p < 0.05), positive results
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67 [email protected] 66 Handling Multiplicity in Variables Scenario 2Divide Type I Error –Identify two (or more) co-primary variables –Divide the 0.05 experiment-wise Type I error over these co-primary variables, e.g., 0.04 for the 1st, and 0.01 for the 2nd co-primary variable –Trial is positive if at least one of the co-primary variables shows significant, positive results
68 [email protected] 67 Handling Multiplicity in Variables Scenario 3 Sequentially Rejective Procedure –Identify n co-primary variables, e.g., n = 3 –Order obtained p-values Interpret the variable with the highest p-value at the 0.05 level; if significant, then interpret the variable with the 2nd highest p-value at the 0.05/2 level; if positive, then interpret the variable with the smallest p-value at the 0.05/3 level. Test procedure stops when a test is not significant.
69 [email protected] 68 Handling Multiplicity in Variables Scenario 4Hierarchy –Prespecify hierarchy among n co-primary variables, –All tested at the same level interpret 1st variable at 0.05 level, if significant, then interpret 2nd variable at 0.05 level; if positive, then interpret 3rd variable at 0.05 level. … Test procedure stops when a test is not significant. –Trial is positive if first co-primary variable shows significant, positive result
70 [email protected] 69 Secondary Variables Secondary Variables Secondary variables can only be claimed if and only if –the primary variable shows significant results, and –the comparisons related to the secondary variables also are protected under the same Type I error rate as the primary variable. Similar procedures as already discussed can be used to protect Type I error
71 [email protected] 70 Handling Multiplicity in Treatments Similar procedures as how to handle multiplicity in variables. Additional procedures are available, mainly geared to very specific settings of the statistical hypotheses. –Dunnett, Scheffee, REGW, Williams …
72 [email protected] 71 SUBGROUPS
73 [email protected] 72 Subgroups Indiscriminate subgroup analyses pose serious multiplicity concerns. Problems reverberate throughout the medical literature. Even after many warnings, some investigators doggedly persist in undertaking excessive subgroup analyses. Lancet 2000; 355: 1033–34 Lancet 2005; 365: 1657–61
74 [email protected] 73 Interacción Edad < 45 años Edad >= 45 años d=5 % d=0.7% d=11.5%
75 [email protected] 74 Factores de confusión No fumadores Fumadores d=6% d=0%
76 [email protected] 75 Subgroups & Simpson’s Paradox
77 [email protected] 76 Subgroups & Simpson’s Paradox cont.
78 [email protected] 77 Subgroups AspirinPlacebo Vascular Death150 147 Total 1357 1442 11.1%10.2% p=0.42045d=-0.9 ISIS-2: Vascular death by Star signs Geminis/LibraOther Star Signs AspirinPlacebo Vascular Death 654 868 Total 7228 7157 9.0% 12.1% p
79 [email protected] 78 Changes from ISIS-2 results Lancet 2005; 365: 1657–61
80 [email protected] 79 “The answer to a randomized controlled trial that does not confirm one’s beliefs is not the conduct of several subanalyses until one can see what one believes. Rather, the answer is to re- examine one’s beliefs carefully.” –BMJ 1999; 318: 1008–09.
81 [email protected] 80 Lancet 2005; 365: 1657–61
82 [email protected] 81 the question is NOT: ‘Is the treatment effect in this subgroup statistically significantly different from zero?’ BUT… are there any differences in the treatment effect between the various subgroups? The correct statistical procedures are either a test of heterogeneity or a test for interaction
83 [email protected] 82 Subgroups Recommendations: –1) Examine the global effect –2) Test for the interaction –3) Plan adjustments for confirmatory analyses –4) Some points which increase the credibility: Pre-specification Biologic plausibility
84 [email protected] 83 Lancet 2005; 365: 176–86
85 [email protected] 84 MULTIPLE INSPECTIONS
86 [email protected] 85 Interim Analyses in the CDP Z Value +2+10-2+2+10-2 10 20 30 40 50 60 70 80 90 100 Month of Follow-up (Month 0 = March 1966, Month 100 = July 1974) Coronary Drug Project Mortality Surveillance. Circulation. 1973;47:I-1 http://clinicaltrials.gov/ct/show/NCT00000483;jsessionid=C4EA2EA9C3351138F8CAB6AFB723820A?order=23
87 [email protected] 86 Lancet 2005; 365: 1657–61
88 [email protected] 87 Tipos de diseño secuencial 1) Reestimación del tamaño muestral 2) Métodos secuenciales por grupos 3) Aproximación por funciones de gasto de 4) Intervalos de confianza repetidos 5) Restricción estocástica 6) Métodos bayesianos 7) Límites continuos (función de verosimilitud)
89 [email protected] 88 Diseño NO aplicable a método secuencial ¿Análisis? Desarrollo total Reclutamiento
90 [email protected] 89 Diseño SÍ aplicable a método secuencial Análisis Desarrollo total Reclutamiento
91 [email protected] 90 Métodos secuenciales por grupos Pocock (1977) Pruebas de significación repetidas K = Nº máximo de inspecciones a realizar K fijo a priori Análisis con pruebas estadísticas clásicas ( 2, t-test,...)
92 [email protected] 91 Group Sequential Methods
93 [email protected] 92 Modelo triangular bilateral
94 [email protected] 93 CPMP/EWP/482/99: PTC on Switching between Superiority and Non- Inferiority & CPMP/EWP/2158/99: PtC on the Choice of Delta
95 [email protected] 94 RANDOMIZATION & COVARIATES
96 [email protected] 95 Adjustement The objective should be not to compensate unbalance (randomisation) but to improve the precision Avoid to adjust by post-randomization variables In RCT, never use this widespread strategy: “adjust by any baseline significant variable (5% or 10% level)”
97 [email protected] 96 Stratification A priori May desire to have treatment groups balanced with respect to prognostic or risk factors (co- variates) For large studies, randomization “tends” to give balance For smaller studies a better guarantee may be needed Useful only to a limited extent (especially for small trials) but avoid to many variables (i.e. many empty or partly filled strata)
98 [email protected] 97 Testing for “baseline homogeneity” All observed differences are known with certainty to be due to chance. We must not test for it: there is no alternative hypothesis whose truth can be supported by such a test. If significant, the estimator is still unbiased Balance: –Decreases the variance and increases the power. –It has no effect on type I error.
99 [email protected] 98 Observed Unbalanced… NEVER justifies the post-hoc adjustment: –Randomization is more important –The treatment effect is unbiased without adjustment (randomization) –Type I error level takes into account for “chance error” –Post-hoc: data driven analyses –Multiplicity issues : increase type I error by allowing a post-hoc adjustment
100 [email protected] 99 Adjusted Analyses ‘ 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.’
101 [email protected] 100 Ajuste por covariables Definición a priori La aparición de desigualdades basales NO justifica el ajuste per se: –Se da más importancia a la randomización –Peligro de los análisis post-hoc –Multiplicidad Como estrategia general, el ajuste por variables significativas basales (ej, p
102 [email protected] 101 Definición de las distintas poblaciones de un estudio
103 [email protected] 102 Objetivo: Evaluar la eficacia de un programa para reducir el peso frente a los a los consejos habituales Diseño: Ensayo Clínico Aleatorio Candidatos: 790 Obesos: 320 Grupo intervención: 161Grupo control: 159 Rechazo: 59 Petición espontánea: 54 Acaban: 102 Acaban: 105
104 [email protected] 103 Grupo intervención: 161Grupo control: 159 Rechazo: 59 Petición espontánea: 54 Acaban: 102 Acaban: 105
105 [email protected] 104 MISSING DATA
106 [email protected] 105 Ex: LOCF & lineal extrapolation 36 32 28 24 - 20 16 12 8 4 0 2 4 6 8 10 12 14 16 18 Time (months) LOCF Lineal Regresion Bias Adas-Cog > Worse < Better
107 [email protected] 106 Ex: Early drop-out due to AE Adas-Cog 36 32 28 24 - 20 16 12 8 4 0 2 4 6 8 10 12 14 16 18 Time (months) Placeb o Active > Worse < Better Bias: Favours Active
108 [email protected] 107 Ex: Early drop-out due to lack of Efficacy Adas-Cog 36 32 28 24 - 20 16 12 8 4 0 2 4 6 8 10 12 14 16 18 Time (months) Placebo Active > Worse < Better Bias: Favours Placebo
109 [email protected] 108 RND B Baseline Last Visit ≠ Frecuencies A Drop-outs and missing data AAAA AA B B A Visit 2 Visit 1 A
110 [email protected] 109 RND Baseline Last Visit ≠ Timing A Drop-outs and missing data AAAAB B Visit 2 Visit 1 BBB
111 [email protected] 110 MD e incorrecto uso de poblaciones (1) Diseño Cirugía vs Tratamiento Médico en estenosis carotidea bilateral (Sackket et al., 1985) Variable principal: Número de pacientes que presenten TIA, ACV o muerte Distribución de los pacientes: Pacientes randomizados:167 Tratamiento quirúrgico: 94 Tratamiento médico: 73 –Pacientes que no completaron el estudio debido a ACV en las fases iniciales de hospitalización: Tratamiento quirúrgico: 15 pacientes Tratamiento médico: 01 pacientes
112 [email protected] 111 MD e incorrecto uso de poblaciones (2) Población Por Protocolo (PP): Pacientes que hayan completado el estudio Análisis –Tratamiento quirúrgico:43 / (94 - 15) = 43 / 79 = 54% –Tratamiento médico:53 / (73 - 1) = 53 / 72 = 74% –Reducción del riesgo:27%, p = 0.02 Primer análisis que se realiza :
113 [email protected] 112 MD e incorrecto uso de poblaciones (3) El análisis definitivo queda de la siguiente forma : Población Intención de Tratar (ITT): Todos los pacientes randomizados Análisis –Tratamiento quirúrgico:58 / 94 = 62% –Tratamiento médico:54 / 73 = 74% –Reducción del riesgo:18%, p = 0.09 (PP: 27%, p = 0.02) Conclusiones: La población correcta de análisis es la ITT El tratamiento quirúrgico no ha demostrado ser significativamente superior al tratamiento médico
114 [email protected] 113 Handling of MD Methods for imputation: –Many techniques –No gold standard for every situation –In principle, all methods may be valid: Simple methods to more complex: –From LOCF to multiple imputation methods –Worst Case, “Mean methods” Multiple Imputation But their appropriateness has to be justified Statistical approaches less sensitive to MD: –Mixed models –Survival models They assume no relationship between treatment and the missing outcome, and generally this cannot be assumed.
115 [email protected] 114 CONCLUSION
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119 [email protected] 118 JAMA 2002; 287: 1807-1814
120 [email protected] 119 Effect Size & Sample Size Relative Effect Absolute Size Power* difference (%) (%) (mmHg) ----------------------------------- 0% 4.9% 0.0 10% 5.9% 0.2 20% 8.5% 0.4 30% 13.3% 0.6 40% 20.2% 0.8 50% 28.2% 1.0 60% 39.3% 1.2 70% 49.3% 1.4 80% 61.1% 1.6 90% 71.0% 1.8 100% 80.4% 2.0 ----------------------------------- * Statistical power assuming constant variability (SD=20mmHg)
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122 [email protected] 121 CPMP/EWP/482/99: PTC on Switching between Superiority and Non- Inferiority & CPMP/EWP/2158/99: PtC on the Choice of Delta
123 [email protected] 122 ENSAYOS DE NO-INFERIORIDAD NECESIDAD Implicaciones legales. Implicaciones metodológicas. Limitaciones éticas y prácticas al uso de placebo. Limitaciones prácticas a la superioridad frente a control activo. Necesidad de información comparativa. Posibles valores añadidos.
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125 [email protected] 124 ENSAYOS DE NO-INFERIORIDAD NECESIDAD Implicaciones legales. Implicaciones metodológicas. Limitaciones éticas y prácticas al uso de placebo. Limitaciones prácticas a la superioridad frente a control activo. Necesidad de información comparativa. Posibles valores añadidos.
126 [email protected] 125 Aproximación con el Poder (prueba clásica + cálculo del poder)
127 [email protected] 126 ENSAYOS DE NO-INFERIORIDAD NECESIDAD Implicaciones legales. Implicaciones metodológicas. Limitaciones éticas y prácticas al uso de placebo. Limitaciones prácticas a la superioridad frente a control activo. Necesidad de información comparativa. Posibles valores añadidos.
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129 [email protected] 128 ENSAYOS DE NO-INFERIORIDAD NECESIDAD Implicaciones legales. Implicaciones metodológicas. Limitaciones éticas y prácticas al uso de placebo. Limitaciones prácticas a la superioridad frente a control activo. Necesidad de información comparativa. Posibles valores añadidos.
130 [email protected] 129 Lancet 2001,356: 1668-75
131 [email protected] 130 ENSAYOS DE NO-INFERIORIDAD NECESIDAD Implicaciones legales. Implicaciones metodológicas. Limitaciones éticas y prácticas al uso de placebo. Limitaciones prácticas a la superioridad frente a control activo. Necesidad de información comparativa. Posibles valores añadidos.
132 [email protected] 131 Valores añadidos Posología: 1 vez al día Vía: vía oral Seguridad: Acontecimientos adversos Poblaciones especiales: Ancianos, pediatría Interacciones
133 [email protected] 132 Ensayos de Equivalencia Ensayos de bioequivalencia (producto genérico vs comercializado) Nuestro producto no es peor y puede presentar otras ventajas (seguridad, comodidad posológica …) –No-inferioridad
134 [email protected] 133 ESTUDIO DE SUPERIORIDAD d > 0 + efecto IC95% d = 0 No hay diferencia d < 0 - efecto Mejor TestMejor Control
135 [email protected] 134 ESTIMACIÓN POR INTERVALO (ESTUDIO DE SUPERIORIDAD) Es estadísticamente significativa d = 0 No hay diferencia d < 0 - efecto d > 0 + efecto IC95% Mejor TestMejor Control
136 [email protected] 135 ESTIMACIÓN POR INTERVALO (ESTUDIO DE SUPERIORIDAD) Es estadísticamente significativa con P=0,05 (justo en el límite) d > 0 + efecto d = 0 No hay diferencia d < 0 - efecto IC 95% Mejor TestMejor Control
137 [email protected] 136 ESTUDIO DE EQUIVALENCIA d > 0 + efecto d = 0 No hay diferencia d < 0 - efecto -d +d Región de equivalencia clínica Delta: ( ) mayor diferencia sin relevancia clínicamayor diferencia sin relevancia clínicao la menor diferencia con relevancia clínicala menor diferencia con relevancia clínica
138 [email protected] 137 EQUIVALENCIA 0 Equivalencia No equivalencia
139 [email protected] 138 NO-INFERIORIDAD TERAPÉUTICA No-Inferioridad No No-Inferioridad 0-- Mejor TestMejor Control
140 [email protected] 139 30% B A P 1/2 ? 1/3 ?
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143 [email protected] 142 30%