Textbook of Psychiatric Epidemiology

Textbook in Psychiatric Epidemiology

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

Textbook in Psychiatric Epidemiology Edited by

Ming T. Tsuang Center for Behavioral Genomics, Department of Psychiatry, University of California, Harvard Institute of Psychiatric Epidemiology & Genetics, Harvard School of Public Health, Boston, USA

Mauricio Tohen Department of Psychiatry, University of Texas Health Science Centre at San Antonio, USA

Peter B. Jones Department of Psychiatry, University of Cambridge, UK

THIRD EDITION

A John Wiley & Sons, Ltd., Publication

This edition first published 2011, © 2011 John Wiley & Sons, Ltd. Wiley-Blackwell is an imprint of John Wiley & Sons, formed by the merger of Wiley’s global Scientific, Technical and Medical business with Blackwell Publishing. Registered office: John Wiley & Sons Ltd, The Atrium, Southern Gate, Chichester, West Sussex, PO19 8SQ, UK Other Editorial Offices: 9600 Garsington Road, Oxford, OX4 2DQ, UK 111 River Street, Hoboken, NJ 07030-5774, USA For details of our global editorial offices, for customer services and for information about how to apply for permission to reuse the copyright material in this book please see our website at www.wiley.com/wiley-blackwell The right of the author to be identified as the author of this work has been asserted in accordance with the Copyright, Designs and Patents Act 1988. All rights reserved. No part of this publication may be reproduced, stored in a retrieval system, or transmitted, in any form or by any means, electronic, mechanical, photocopying, recording or otherwise, except as permitted by the UK Copyright, Designs and Patents Act 1988, without the prior permission of the publisher. Wiley also publishes its books in a variety of electronic formats. Some content that appears in print may not be available in electronic books. Designations used by companies to distinguish their products are often claimed as trademarks. All brand names and product names used in this book are trade names, service marks, trademarks or registered trademarks of their respective owners. The publisher is not associated with any product or vendor mentioned in this book. This publication is designed to provide accurate and authoritative information in regard to the subject matter covered. It is sold on the understanding that the publisher is not engaged in rendering professional services. If professional advice or other expert assistance is required, the services of a competent professional should be sought. The contents of this work are intended to further general scientific research, understanding, and discussion only and are not intended and should not be relied upon as recommending or promoting a specific method, diagnosis, or treatment by physicians for any particular patient. The publisher and the author make no representations or warranties with respect to the accuracy or completeness of the contents of this work and specifically disclaim all warranties, including without limitation any implied warranties of fitness for a particular purpose. In view of ongoing research, equipment modifications, changes in governmental regulations, and the constant flow of information relating to the use of medicines, equipment, and devices, the reader is urged to review and evaluate the information provided in the package insert or instructions for each medicine, equipment, or device for, among other things, any changes in the instructions or indication of usage and for added warnings and precautions. Readers should consult with a specialist where appropriate. The fact that an organization or Website is referred to in this work as a citation and/or a potential source of further information does not mean that the author or the publisher endorses the information the organization or Website may provide or recommendations it may make. Further, readers should be aware that Internet Websites listed in this work may have changed or disappeared between when this work was written and when it is read. No warranty may be created or extended by any promotional statements for this work. Neither the publisher nor the author shall be liable for any damages arising herefrom. Library of Congress Cataloguing-in-Publication Data Textbook of psychiatric epidemiology / [edited by] Ming T. Tsuang, Mauricio Tohen, Peter B. Jones. – 3rd ed. p. ; cm. Rev. ed. of: Textbook in psychiatric epidemiology / edited by Ming T. Tsuang, Mauricio Tohen. 2nd ed. c2002. Includes bibliographical references and index. ISBN 978-0-470-69467-1 (cloth) 1. Psychiatric epidemiology. I. Tsuang, Ming T., 1931- II. Tohen, Mauricio, 1951- III. Jones, Peter B. (Peter Brian), 1960IV. Textbook in psychiatric epidemiology. [DNLM: 1. Epidemiologic Methods. 2. Mental Disorders–epidemiology. 3. Mental Disorders–diagnosis. WM 140] RC455.2.E64T49 2011 362.2 0422–dc22 2010046396 ISBN: 978-0-470-69467-1 A catalogue record for this book is available from the British Library. This book is published in the following electronic formats: ePDF: 978-0-470-97672-2; Wiley Online Library: 978-0-470-97673-9; ePub: 978-0-470-97740-8. Set in 9/12pt Sabon by Laserwords Private Limited, Chennai, India First

2011

Contents

List of Contributors, xi 1 Introduction to epidemiologic research methods, 1 Glyn Lewis 1.1 What is epidemiology? 1 1.2 Causation in medicine, 2 1.3 Causal inference, 6 1.4 The future for psychiatric epidemiology, 7 References, 7 2 Analysis of categorical data: The odds ratio as a measure of association and beyond, 9 Garrett M. Fitzmaurice and Caitlin Ravichandran 2.1 Introduction, 9 2.2 Inference for a single proportion, 10 2.3 Analysis of 2 × 2 contingency tables, 11 2.4 Analysis of sets of 2 × 2 contingency tables, 16 2.5 Logistic regression, 18 2.6 Advanced topics, 25 2.7 Concluding remarks, 29 2.8 Further reading, 29 References, 29 3 Genetic epidemiology, 31 Stephen V. Faraone, Stephen J. Glatt and Ming T. Tsuang 3.1 Introduction, 31 3.2 The chain of psychiatric genetic research, 31 3.3 Psychiatric genetics and psychiatric epidemiology, 44 Acknowledgements, 45

References, 45 Further reading, 47 4 Examining gene–environment interplay in psychiatric disorders, 53 Judith Allardyce and Jim van Os 4.1 Introduction, 53 4.2 The process of genetic epidemiology, 54 4.3 Gene–environment interplay takes different forms, 55 4.4 Gene–environment correlation, 55 4.5 Gene–environment interaction, 58 4.6 Measurement of genotype, environmental exposure and pathological phenotype, 58 4.7 Models of GxE, 60 4.8 Which scale should we use to measure GxE? 61 4.9 Study designs for the detection of GxE, 62 4.10 Threats to the validity of epidemiological GxE studies, 65 4.11 Epigenetic mechanisms, 67 References, 67 5 Reliability, 73 Patrick E. Shrout 5.1 Introduction, 73 5.2 The reliability coefficient, 73 5.3 Designs for estimating reliability, 74 5.4 Statistical remedies for low reliability, 76 5.5 Reliability theory and binary judgements, 77 5.6 Reliability statistics: General, 78 5.7 Other reliability statistics, 82 5.8 Summary and conclusions, 83 References, 83

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CONTENTS

6 Moderators and mediators: Towards the genetic and environmental bases of psychiatric disorders, 87 Helena Chmura Kraemer 6.1 Introduction, 87 6.2 Current methodological barriers, 89 6.3 Moderation, mediation and other ways in which risk factors ‘work together’, 92 6.4 Extensions, 94 6.5 Beyond moderators and mediators, 95 References, 96 7 Validity: Definitions and applications to psychiatric research, 99 Jill M. Goldstein, Sara Cherkerzian and John C. Simpson 7.1 Introduction, 99 7.2 Validity of a construct, 99 7.3 Validity of the relationships between variables, 110 7.4 Summary, 112 Acknowledgements, 113 References, 113 8 Use of register data for psychiatric epidemiology in the Nordic countries, 117 Jouko Miettunen, Jaana Suvisaari, Jari Haukka and Matti Isohanni 8.1 Introduction, 117 8.2 Registers for use in psychiatric research, 118 8.3 Register research in Denmark, 122 8.4 Register research in Finland, 123 8.5 Register research in Norway, 124 8.6 Register research in Sweden, 125 8.7 Discussion, 126 Acknowledgements, 127 References, 127 9 An introduction to mental health services research, 133 ´ Anna Fernandez, Alejandra Pinto-Meza, Antoni Serrano-Blanco, Jordi Alonso and Josep Maria Haro 9.1 Introduction, 133 9.2 What is mental health services research? 134 9.3 A framework for mental health services research, 135 vi

9.4 Key concepts in mental health services research, 137 9.5 Examples of mental health services research studies, 141 9.6 Conclusion, 152 References, 152 10 The pharmacoepidemiology of psychiatric medications, 155 Philip S. Wang, Alan M. Brookhart, Christine Ulbricht and Sebastian Schneeweiss 10.1 Introduction, 155 10.2 Overview of psychopharmacoepidemiology, 156 10.3 Sources of data, 157 10.4 Examples of recent psychopharmacoepidemiologic studies, 159 10.5 Conclusions, 162 Acknowledgements, 163 References, 163 11 Peering into the future of psychiatric epidemiology, 167 Michaeline Bresnahan, Ezra Susser, Dana March and Bruce Link 11.1 Introduction, 167 11.2 Levels of causation: A historical overview, 167 11.3 Levels of causation, 169 11.4 Causation over (life) time, 172 11.5 Examples, 174 11.6 Framing the future, 178 References, 179 12 Studying the natural history of psychopathology, 183 William W. Eaton 12.1 Introduction, 183 12.2 Onset, 183 12.3 Course, 188 12.4 Outcome, 191 12.5 Methodological concepts for studying the natural history of psychopathology, 192 12.6 Conclusion, 195 Acknowledgements, 195 References, 195

CONTENTS

13 Symptom scales and diagnostic schedules in adult psychiatry, 199 Jane M. Murphy 13.1 Introduction, 199 13.2 North American instruments for epidemiological research, 202 13.3 North American instruments for psychiatric services and primary care, 205 13.4 European instruments for psychiatric services and primary care, 206 13.5 European instruments for epidemiological research, 208 13.6 Summary, 210 Acknowledgements, 212 References, 212 14 The National Comorbidity Survey (NCS) and its extensions, 221 Ronald C. Kessler 14.1 Introduction, 221 14.2 The baseline NCS, 221 14.3 The NCS follow-up survey (NCS-2), 227 14.4 The NCS replication survey (NCS-R), 229 14.5 The NCS-R adolescent supplement (NCS-A), 233 14.6 The WHO WMH Surveys, 234 14.7 Overview, 236 Acknowledgements, 237 References, 237 15 Experimental epidemiology, 243 John R. Geddes 15.1 Introduction, 243 15.2 Limitations of non-randomised evidence, 243 15.3 RCTs: The translation of the experimental design into the real world, 245 15.4 Importance and control of systematic error or bias, 245 15.5 Importance and control of random error and noise, 248 15.6 Reporting the results of clinical trials—the CONSORT statement, 248 15.7 Different clinical questions will prioritise control of different threats to validity and confidence, 248

15.8 The classification of RCTs, 251 15.9 Effectiveness trials in schizophrenia, 255 15.10 Department of Veterans Affairs co-operative study on the cost-effectiveness of Olanzapine (Rosenheck), 255 15.11 The clinical antipsychotic trials of intervention effectiveness (CATIE) study, 257 15.12 Cost utility of the latest antipsychotic drugs in schizophrenia study (CUtLASS 1), 257 15.13 European first-episode schizophrenia trial (EUFEST), 258 15.14 The size and cost of experimental studies in psychiatry, 259 15.15 Clinical trials in the future, 259 References, 259 16 Epidemiology of Schizophrenia, 263 William W. Eaton, Chuan-Yu Chen and Evelyn J. Bromet 16.1 Introduction, 263 16.2 Methods, 263 16.3 The burden of schizophrenia, 264 16.4 Natural history, 265 16.5 Demographic correlates, 268 16.6 Social risk factors, 269 16.7 Biological risk factors, 272 16.8 Prevention, 279 16.9 Discussion, 280 References, 280 17 Epidemiology of depressive disorders, 289 Deborah S. Hasin, Miriam C. Fenton and Myrna M. Weissman 17.1 Introduction, 289 17.2 Major depression, 290 17.3 Dysthymia, 302 17.4 Summary, 304 Appendix 17.A Measurement of major depression in the NLAES and NESARC, 304 References, 305 18 Epidemiology of anxiety disorders, 311 Ewald Horwath, Felicia Gould and Myrna M. Weissman 18.1 Introduction, 311 vii

CONTENTS

18.2 18.3 18.4 18.5 18.6 18.7 18.8

Anxiety disorders, 311 Panic disorder, 313 Agoraphobia, 316 Social phobia, 317 Generalised anxiety disorder, 318 Obsessive–compulsive disorder, 319 Anxiety and affective disorders and mass disasters, 320 18.9 Future developments, 323 Acknowledgements, 323 References, 323 Further reading, 326 19 Epidemiology of bipolar disorder in adults and children, 329 Kathleen R. Merikangas and Mauricio Tohen 19.1 Introduction, 329 19.2 Epidemiology of bipolar disorder, 329 19.3 Patterns of comorbidity of bipolar disorder, 333 19.4 Risk Factors, 334 19.5 Future directions, 336 19.6 Summary, 338 References, 338 20 Epidemiology of eating disorders, 343 Tracey D. Wade, Anna Keski-Rahkonen and James I. Hudson 20.1 Introduction, 343 20.2 Case definition, 343 20.3 Major prevalence studies, 345 20.4 Incidence studies, 351 20.5 Comorbidity, 351 20.6 Mortality from eating disorders, 352 20.7 Risk factors, 352 20.8 Future directions, 355 References, 356 21 Epidemiology of alcohol use, abuse and dependence, 361 Deborah A. Dawson, Ralph W. Hingson and Bridget F. Grant 21.1 Introduction, 361 21.2 Population estimates of per capita consumption, 361 21.3 Survey-based estimates of the prevalence of drinking, 362 21.4 Alcohol-related mortality and morbidity, 365 viii

21.5 Alcohol and injury, 365 21.6 Alcohol and chronic disease, 366 21.7 Diagnostic classification of alcohol use disorders, 367 21.8 Population estimates, prevalence, incidence and natural course of alcohol use disorders, 368 21.9 Comorbidity of DSM-IV alcohol use disorders and other psychiatric disorders, 371 21.10 Summary, 374 Acknowledgements, 375 References, 375 22 Epidemiology of illicit drug use disorders, 381 Wilson M. Compton, Marsha F. Lopez, Kevin P. Conway and Yonette F. Thomas 22.1 Introduction, 381 22.2 Drug consumption, 381 22.3 Definitions, 384 22.4 Rates of DSM-IV abuse and dependence, 384 22.5 Global rates of drug use disorders, 387 22.6 Comorbidities with psychiatric conditions, 388 22.7 Genetic epidemiology, 391 22.8 Future opportunities, 391 22.9 Conclusions, 394 22.10 Disclaimer, 394 References, 394 23 The epidemiology of personality disorders: Findings, methods and concepts, 401 Michael J. Lyons, Beth A. Jerskey and Margo R. Genderson 23.1 Introduction, 401 23.2 Substantive findings, 402 23.3 Course, prognosis and developmental issues, 404 23.4 Treated prevalence, 406 23.5 Prevalence of specific personality disorders, 407 23.6 Antisocial personality disorder, 410 23.7 Conceptual issues, 419 23.8 Models of personality disorder, 419 23.9 Methodological issues, 422 23.10 Future directions, 427 References, 428

CONTENTS

24 The epidemiology of depression and anxiety in children and adolescents, 435 Kathleen Ries Merikangas and Erin F. Nakamura 24.1 Introduction, 435 24.2 Magnitude of depression and anxiety in children and adolescents, 435 24.3 Correlates and risk factors, 438 24.4 Service patterns and impact, 442 24.5 Summary, 443 References, 443 25 Epidemiology of attention deficit hyperactivity disorder, 449 Stephen V. Faraone 25.1 Introduction, 449 25.2 Prevalence of ADHD, 450 25.3 Pharmacoeconomics of ADHD, 451 25.4 Comorbid psychiatric disorders, 451 25.5 Demographic risk factors, 452 25.6 Genetic risk factors, 453 25.7 Environmental risk factors for ADHD, 457 25.8 Summary and conclusions, 460 25.9 Future directions, 460 Acknowledgements, 461 References, 461 26 The epidemiology of autism, 469 Gregory S. Liptak 26.1 Introduction, 469 26.2 Background, 469 26.3 Definition and diagnosis, 469 26.4 Natural history, 472 26.5 Prevalence, 473 26.6 Risk factors, 473 26.7 Genetic factors, 476 26.8 Public health impact, 476 26.9 Associations and causal factors, 477 26.10 Future directions, 477 26.11 Summary, 478 References, 478 27 Mental illness, women, mothers and their children, 483 Kathryn M. Abel and Vera A. Morgan 27.1 Introduction, 483

27.2 The epidemiology of mental illness in women of reproductive age, 484 27.3 Fertility and fecundity in women with mental illness, 487 27.4 Maternal mental illness at the time of conception and during pregnancy, 488 27.5 Gene–environment interactions and offspring outcomes, 493 27.6 Obstetric complications and risk of adult onset mental disorder in offspring, 493 27.7 Parental condition, 496 27.8 Motherhood and perinatal mental illness, 500 27.9 Designing studies examining the relationship between maternal mental illness and outcomes for their children, 504 27.10 Conclusions, 507 References, 507 Further reading, 515 28 Epidemiology of suicide and attempted suicide, 517 Dianne Currier and Maria A. Oquendo 28.1 Introduction, 517 28.2 Definitions, 517 28.3 Prevalence of suicide and attempted suicide, 518 28.4 Risk factors for suicide and attempted suicide, 520 28.5 Protective factors, 526 28.6 Conclusions, 526 Acknowledgements, 526 References, 526 29 Epidemiology and geriatric psychiatry, 535 Celia F. Hybels and Dan G. Blazer 29.1 Introduction, 535 29.2 Issues of case identification, 535 29.3 The distribution of cases, 536 29.4 Aetiological studies, 544 29.5 Outcome studies, 547 29.6 Historical trends in the epidemiology of psychiatric disorders in late life, 549 29.7 Use of health care services, 550 References, 550 ix

CONTENTS

30 Recent epidemiological studies of psychiatric disorders in Japan, 559 Masayoshi Kawai, Kenji J. Tsuchiya and Nori Takei 30.1 Introduction, 559 30.2 Schizophrenia, 560 30.3 Affective disorders, 566 30.4 Autism and autism spectrum disorder, 569 30.5 Summary, 572 References, 573 31 Epidemiology of migration and serious mental illness: The example of migrants to Europe, 579 Monica Charalambides, Craig Morgan and Robin M. Murray 31.1 Introduction, 579 31.2 Defining the constructs, 579 31.3 High rates of psychosis in migrants: A genuine finding or methodological artefact?, 581 31.4 Possible explanations, 584 31.5 Biological considerations, 585 31.6 Cannabis use, 586 31.7 Adverse social experiences, 586 31.8 Mechanisms, 589 31.9 Implications, 590 References, 591 32 Epidemiology of migration substance use disorder in Latin American populations and migration to the United States, 595 Mar´ıa Elena Medina-Mora, Guilherme Borges, Tania Real and Jorge Villatoro 32.1 Introduction, 595

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32.2 Definitions: What do we understand by migration?, 595 32.3 Countries of origin: Social, political and other reasons that trigger migration, 597 32.4 Living conditions of migrants in the United States, 599 32.5 Alcohol and drug use in countries of origin and receiving communities, 600 32.6 Dependence and treatment rates, 604 32.7 The process of migrating, 606 32.8 Migration, substance use and access to services, 608 32.9 Returning migrants and families left behind, 611 32.10 Conclusions, 611 References, 611 33 Early detection and intervention as approaches for preventing schizophrenia, 617 Ming T. Tsuang, William S. Stone, Margo Genderson and Michael Lyons 33.1 Introduction, 617 33.2 Modelling genetic and phenotypic heterogeneity, 618 33.3 Defining a syndrome of liability using cognitive and clinical characteristics of relatives, 620 33.4 Gene-based vs. genome-based research, 624 33.5 Future directions, 626 33.6 Clinical implications, 627 Acknowledgements, 627 References, 628 Index, 633

List of Contributors

Kathryn M. Abel

Monica Charalambides

Centre for Women’s Mental Health, 3rd Floor East, Jean McFarlane Bdg, University of Manchester, Oxford Road, Manchester M13 9PL, UK

Institute of Psychiatry, Psychological Medicine, King’s Institute, De Crespigny Park, Denmark Hill, London SE5 8AF, UK

Judith Allardyce

Chuan-Yu Chen

Department of Psychiatry and Neuropsychology, School for Mental Health and Neuroscience, South Limburg Mental Health Research and Teaching Network, EURON, SEARCH, Maastricht University Medical Centre, PO BOX 616 (VIJV), 6200 MD Maastricht, The Netherlands

National Health Research Institutes, Institute of Population Health Sciences, Division of Mental Health and Addiction Medicine, Taiwan

Jordi Alonso Carrer del Doctor Aiguader, 88, Edifici PRBB, E-08003 Barcelona, Spain

Dan G. Blazer Department of Psychiatry and Behavioral Sciences, Center for the Study of Aging and Human Development, Box 3003, Duke University Medical Center, Durham NC 27710, USA

Guilherme Borges Ramon de la Fuente National Institute of Psychiatry, Calzada Mexico Xochimilco 101, DF 14370, Mexico

Michaeline Bresnahan Mailman School of Public Health, Columbia University, Department of Epidemiology, 600 West 168th Street, New York NY 10032, USA

Evelyn J. Bromet Dept of Psychiatry, SUNY Stony Brook University, PutnamHall – South Campus, Stony Brook NY 11794-8790, USA

Alan M. Brookhart Division of Pharmacoepidemiology and Pharmacoeconomics, Brigham and Women’s Hospital, Harvard Medical School, Boston MA 02115, USA

Sara Cherkerzian Departments of Psychiatry and Medicine at Brigham and Women’s Hospital (BWH), Harvard Medical School, Boston, MA, USA

Wilson M. Compton Division of Epidemiology, Services, and Prevention Research, National Institute on Drug Abuse, 6001 Executive Blvd., MSC 9589, Bethesda MD 20892-9589, USA

Kevin P. Conway Division of Epidemiology, Services, and Prevention Research, National Institute on Drug Abuse, 6001 Executive Blvd., MSC 9589, Bethesda MD 20892-9589, USA

Dianne Currier Division of Molecular Imaging and Neuropathology, Department of Psychiatry, Columbia University, New York, NY 10032, USA

Deborah A. Dawson Laboratory of Epidemiology and Biometry, Division of Intramural Clinical and Biological Research, National Institute on Alcohol Abuse and Alcoholism, National Institutes of Health, Suite 514, Willco Building, 6000 Executive Boulevard, MSC 7003, Bethesda MD 20892-7003, USA

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LIST OF CONTRIBUTORS

William W. Eaton Dept of Mental Health, Bloomberg School of Public Health, John Hopkins School of Hygiene and Public Health, John Hopkins University, 615 N. Wolfe Street, Baltimore MD 21205, USA

Stephen V. Faraone Center for NeuroPsychiatric Genetics, SUNY Upstate Medical University, Weiskotten Hall 3285, Syracuse NY 13210, USA

Miriam C. Fenton New York State Psychiatric Institute 1051 Riverside Drive, New York, NY 10032, USA

´ Anna Fernandez Fundac´ıo Sant Joan de D´eu Research and Development Unit, Dr. Antoni Pujadas, 42., 08830 Sant Boi de Llobregat, Barcelona, Spain

Garrett Fitzmaurice Laboratory for Psychiatric Biostatistics, McLean Hospital, Belmont, MA, USA

Institutes of Health, NIAAA/LEB, 5635 Fishers Lane, Bethesda MD 20892-9304, USA

Josep Maria Haro Fundacı´o Sant Joan de D´eu Research and Development Unit, Dr. Antoni Pujadas, 42., 08830 Sant Boi de Llobregat, Barcelona, Spain

Deborah S. Hasin Department of Psychiatry, Columbia University College of Physicians and Surgeons, New York NY 10032, USA

Jari Haukka National Institute for Health and Welfare, Department of Mental Health and Substance Abuse Services, P.O. Box 30, FI 00271 Helsinki, Finland

Ralph W. Hingson Division of Epidemiology and Prevention Research, National Institute on Alcohol Abuse and Alcoholism, National Institutes of Health, NIAAA/LEB, 5635 Fishers Lane, Bethesda MD 20892-9304, USA

Ewald Horwath John R. Geddes Oxford University, Department of Psychiatry, Warneford Hospital, Oxford OX3 7JX, UK

Margo R. Genderson Department of Psychology, Boston University, Boston, MA 02215, USA

Stephen J. Glatt Departments of Psychiatry and Behavioral Sciences and Neuroscience and Physiology, Medical Genetics Research Center, SUNY Upstate Medical University, NY, USA

Jill M. Goldstein Departments of Psychiatry and Medicine at Brigham and Women’s Hospital (BWH), Harvard Medical School, Boston MA02115, USA

Department of Psychiatry, Epidemiology and Public Health, Miller School of Medicine, University of Miami, MHHC, Suite 3100, 1695 NW 9th Ave, Miami FL 33136, USA

James I. Hudson Psychiatric Epidemiology Research Program, Harvard Medical School/McLean Hospital, 115 Mill Street, Belmont MA 02478, USA

Celia F. Hybels Department of Psychiatry and Behavioral Sciences, Center for the Study of Aging and Human Development, Duke University Medical Center, Box 3003, Durham NC 27710, USA

Matti Isohanni Department of Psychiatry, University of Oulu, Finland

Felicia Gould Department of Psychiatry & Behavioral Sciences, Miller School of Medicine, University of Miami, 3225 Aviation Ave., Suite 303, Miami FL 33133, USA

Bridget F. Grant Laboratory of Epidemiology and Biometry, Division of Intramural Clinical and Biological Research, National Institute on Alcohol Abuse and Alcoholism, National

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Beth A. Jerskey Instructor of Psychiatry and Human Behavior (Research), Alpert Medical School of Brown University, Providence RI 02912, USA

Peter B. Jones Department of Psychiatry, University of Cambridge, Box 189, Addenbrooke’s Hospital, Cambridge CB2 2QQ, UK

LIST OF CONTRIBUTORS

Masayoshi Kawai

Kathleen R. Merikangas

Research Centre for Child Mental Development, Hamamatsu University School of Medicine 1-20-1, Handayama, Higashi-Ku, Hamamatsu 431–3192, Japan

Genetic Epidemiology Research Branch, Intramural Research Program, NIMH, Porter Neuroscience Research Center, 35 Convent Dr., MSC 3720, Bethesda MD 20892-3720, USA

Anna Keski-Rahkonen

Jouko Miettunen

Academy of Finland, University of Helsinki, Helsinki, Finland

Department of Psychiatry, University of Oulu, P.O.Box 5000, FI-90014 Helsinki, Finland

Ronald C. Kessler

Craig Morgan

Department of Health Care Policy, Harvard Medical School, 180 Longwood Avenue, Boston MA 02115, USA

Institute of Psychiatry, Psychological Medicine, King’s Institute, De Crespigny Park, Denmark Hill, London SE5 8AF, UK

Helena Chmura Kraemer

Vera A. Morgan

Department of Psychiatry, Stanford University, Palo Alto, Stanford CA 94305, USA

Neuropsychiatric Epidemiology Research Unit, School of Psychiatry & Clinical Neurosciences, The University of Western Australia, Medical Research Foundation Building, 50 Murray Street, Perth, WA 6000, Australia

Glyn Lewis Academic Unit of Psychiatry,University of Bristol, Cotham House, Cotham Hill, Bristol BS6 6JL, UK

Jane M. Murphy Bruce Link Mailman School of Public Health, Columbia University, Department of Epidemiology, 600 West 168th Street, New York NY 10032, USA

Greg S. Liptak Center for Development, Behavior and Genetics, SUNY Upstate Medical University, Center for Children’s’ Health Policy, Syracuse NY 13210, USA

Professor, Department of Psychiatry, Massachusetts General Hospital, Harvard Medical School, Room 215, 5 Longfellow Place, Boston MA 02114, USA

Robin M. Murray Institute of Psychiatry, Psychological Medicine, King’s Institute, De Crespigny Park, Denmark Hill, London SE5 8AF, UK

Erin F. Nakamura Marsha F. Lopez Division of Epidemiology, Services, and Prevention Research, National Institute on Drug Abuse, 6001 Executive Blvd., MSC 9589, Bethesda, MD 20892-9589, USA

Michael J. Lyons Department of Psychology, Boston University, Harvard Institute of Psychiatric Epidemiology and Genetics, 64 Cummington Street, Boston MA 02215, USA

Dana March Mailman School of Public Health, Columbia University, Department of Epidemiology, 600 West 168th Street, New York NY 10032, USA

Mar´ıa Elena Medina-Mora Ramon de la Fuente National Institute of Psychiatry, Calzada Mexico Xochimilco 101, DF 14370, Mexico

Genetic Epidemiology Research Branch, Intramural Research Program, NIMH, Porter Neuroscience Research Center, 35 Convent Dr., MSC 3720, Bethesda MD 20892-3720, USA

Maria A. Oquendo Division of Molecular Imaging and Neuropathology, Department of Psychiatry, Columbia University, NY, USA

Alejandra Pinto-Meza Fundac´ıo Sant Joan de D´eu Research and Development Unit, Dr. Antoni Pujadas, 42., 08830 Sant Boi de Llobregat, Barcelona, Spain

Antoni Pujadas Fundaci o Sant Joan de Deu Research and Development Unit, Dr. Antoni Pujadas, 42., 08830 Sant Boi de Llobregat, Barcelona, Spain

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LIST OF CONTRIBUTORS

Caitlin Ravichandran

Yonette F. Thomas

Laboratory for Psychiatric Biostatistics, McLean Hospital, 115 Mill St, Belmont MA 02478, USA

Howard University, Office of the Vice President for Research and Compliance (OVPRC), C.B. Powell Building, Suite 137, 525 Bryant Street, N.W., Washington DC 20059, USA

Tania Real Ramon de la Fuente National Institute of Psychiatry, Calzada Mexico Xochimilco 101, DF 14370, Mexico

Mauricio Tohen

Rebeca Robles

Division of Mood and Anxiety Disorders, University of Texas Health Science Center at San Antonio, 7526 Louis Pasteur Drive, San Antonio TX 78229-3900, USA

Ramon de la Fuente National Institute of Psychiatry, Calzada Mexico Xochimilco 101, DF 14370, Mexico

Ming T. Tsuang

Sebastian Schneeweiss Division of Pharmacoepidemiology and Pharmacoeconomics, Brigham and Women’s Hospital, Harvard Medical School, Boston MA02115, USA

Antoni Serrano-Blanco Fundac´ıo Sant Joan de D´eu Research and Development Unit, Dr. Antoni Pujadas, 42., 08830 Sant Boi de Llobregat, Barcelona, Spain

Patrick E. Shrout Department of Psychology, New York University, 6 Washington Place, Rm 455, New York NY 1003, USA

Center for Behavioral Genomics, Department of Psychiatry, University of California, San Diego, 9500 Gilman Drive, La Jolla CA 92039, USA

Kenji J. Tsuchiya Research Centre for Child Mental Development, Hamamatsu University School of Medicine 1-20-1, Handayama, Higashi-Ku, Hamamatsu 431–3192, Japan

Christine Ulbricht Division of Services and Intervention Research, National Institute of Mental Health, 6001 Executive Blvd, Room 7151, MSC 9629, Bethesda MD 20892-9663, USA

Jim van Os John Simpson Department of Psychiatry at VA Boston Healthcare System, Harvard Medical School Department of Psychiatry, Boston MA 02215, USA

William S. Stone

Department of Psychiatry and Neuropsychology, School of Mental Health and Neuroscience, South Limburg Mental Health Research and Teaching Network, Maastricht University Medical Centre, PO Box 616, Vijverdal, 6200 MD, Maastricht, The Netherlands

Harvard Institute of Psychiatric Epidemiology and Genetics, Department of Epidemiology, Harvard School of Public Health, Boston, MA, USA

Jorge Villatoro

Ezra Susser

Tracey D. Wade

Mailman School of Public Health, Columbia University, Department of Epidemiology, 600 West 168th Street, New York NY 10032, USA

School of Psychology, Flinders University, GPO Box 2100, Adelaide SA 5001, Australia

Jaana Suvisaari

Division of Services and Intervention Research, National Institute of Mental Health, 6001 Executive Blvd, Room 7151, MSC 9629, Bethesda, MD 20892-9663, USA

Department of Mental Health and Substance Abuse Services, National Institute for Health and Welfare, P.O.Box 30, FI 0027 Helsinki, Finland

Nori Takei Research Centre of Child Mental Development, Hamamatsu University School of Medicine 1-20-1, Handayama, Higashi-Ku, Hamamatsu 431–3192, Japan

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Ramon de la Fuente National Institute of Psychiatry, Calzada Mexico Xochimilco 101, DF 14370, Mexico

Philip S. Wang

Myrna M. Weissman Department of Psychiatry, Columbia University,College of Physicians and Surgeons, New York State Psychiatric Institute, 1051 Riverside Drive, New York NY 10032, USA

1

Introduction to epidemiologic research methods Glyn Lewis Academic Unit of Psychiatry, University of Bristol, Bristol, UK

1.1 What is epidemiology? Epidemiology, according to Last’s Dictionary of Epidemiology, is ‘The study of the distribution and determinants of health-related states or events in specified populations and the application of this study to control of health problems’ [1]. Wikipedia states ‘Epidemiology is the study of factors affecting the health and illness of populations, and serves as the foundation of interventions made in the interest of public health and preventive medicine’. Rothman and Greenland [2] after observing ‘there seem to be more definitions of epidemiology than epidemiologists’ fulfil their own observation by creating a new definition: ‘the ultimate goal of most epidemiologic research is the elaboration of causes that can explain patterns of disease occurrence’ [2], thereby narrowing the focus of the subject on aetiology. John Snow is usually credited with creating epidemiology as a result of his work in the 1840s associating cholera with contaminated water from the River Thames in London [3]. It was only in the second half of the twentieth century that epidemiological methods began to be consistently applied to the whole range of health problems. Before that time, most of the focus was on infectious disease, though there were exceptions, such as pellagra [4]. Rothman coined the term ‘modern epidemiology’ [5] to reflect the increasing understanding of population based research after the second world war and the increase in its application. The Framingham Heart Study was started in 1949 and Bradford Hill,

amongst his other contributions, conducted the first randomised controlled trial (RCT) in medicine in 1948 [4]. This postwar era is the most important from the perspective of psychiatry. In this period the terms ‘chronic disease epidemiology’ or ‘risk factor epidemiology’ have been used to describe the extension of epidemiological methods to noninfectious disease. It is during this period that, in the main, psychiatric epidemiology has developed, often learning from epidemiologists studying heart disease and cancer. Epidemiologists get involved in studies with a variety of uses [6] including straightforward description, as well as the studies of aetiology that Rothman and Greenland mention in their definition. However, most definitions of epidemiology appear, at least at first sight, to leave out RCTs and systematic reviews yet many epidemiologists also carry out such studies. The use of the term clinical epidemiology [5] reflects this broadening of epidemiological methods into the care of patients, the validity of diagnostic tests and clinical decision making [7]. Epidemiologists have been at the heart of the evidence-based medicine movement [8] and thinking about how research findings are best transferred to clinical practice. And finally, ‘genetic epidemiology’ [6] is the creation of a marriage between epidemiology and genetics. It is designed to exploit molecular genetics and the technological advances that have enabled rapid characterisation of a person’s genetic makeup. Epidemiology has increased its scope and remit within medicine and psychiatric epidemiology is

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

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a reflection of these imperialistic tendencies. At times, it is difficult to decide where epidemiology ends and ‘other’ clinical research begins; it is a matter of emphasis. Epidemiologists tend to be more oriented towards the study of common conditions of public health importance and are more interested in making inferences about whole populations. In epidemiology, there is more emphasis on establishing causal relationships than understanding the mechanisms that might underpin those relationships. Even though, when possible, epidemiological methods are also needed for investigating mechanisms. This concern with causation has led epidemiologists to emphasise the importance of RCTs to evaluate treatments and to summarise evidence using systematic reviews. So perhaps, those definitions of epidemiology quoted above are sufficient and adequately cover the remit and scope of the discipline.

the collection of DNA in epidemiological studies, which is now useful thanks to the massive technological progress in genetics. But for other areas of neuroscience, this is still mostly a challenge for the future. There are examples of population-based studies of brain imaging [9] and neuroendocrinology [10] but epidemiologists will need further assistance from scientists engaged in imaging, psychology and other areas of basic science in order to develop quicker and easier tests to use in population studies and improve understanding of the neuroscientific basis of psychiatric disorder. We should also not forget about social science. Social scientists will also help in understanding the social context of psychiatric disorder, for example the ideas about social capital have been influential [11] though the advances in social science appear less rapid than those in neuroscience.

1.1.1 Psychiatric epidemiology

1.2 Causation in medicine

Psychiatric epidemiology is simply the epidemiology of psychiatric disorders – no more, no less. The principles and practice are the same when studying psychiatric disorder as they are when studying other medical conditions. Understanding the epidemiological principles and methods developed for physical disease will inform our epidemiological study of psychiatric disorder. Good psychiatric practice requires attention paid to biological, psychological and social factors. The same can be said for psychiatric epidemiology. When studying aetiology or evaluating treatments, epidemiological research is testing hypotheses about cause or treatment based upon a theory relating biological, psychological or social factors to illness or recovery. Understanding the mechanisms underlying disease and treatment is therefore critical in interpreting data from epidemiological and clinical studies. However, it is important to acknowledge that epidemiology is often limited in investigating mechanisms as epidemiological studies often involve measurements that are remote from the mechanisms that are likely to be important. This is an especial problem in psychiatry as it is difficult to carry out intensive biological and psychological assessments in the context of large scale epidemiological studies. A recent exception is

One of the most important functions of epidemiology, as suggested by Rothman and Greenland [2] is to investigate factors that might cause disease and treatments or interventions that might cause recovery. Causal inference is the label for a process of reasoning that provides some structure to this difficult and often rather subjective task. ‘Risk factor’ is often used by epidemiologists, in part, to show that there is always some doubt about causal relationships. However, we are only really interested in ‘risk factors’ if they are causal. The first issue to address, then, is what is meant by ‘cause’. Cause is a word, that is used in everyday language but in medicine it is important that this word is defined and understood in a way that distinguishes it from its usual use in language. Rothman [5] has provided one of the most reasoned and influential approaches towards thinking about cause in medicine. He defines cause (of disease) as ‘an event, condition or characteristic that plays an essential role in producing an occurrence of a disease’. In other words, that a particular occurrence of disease would not have occurred without that event/condition/characteristic having happened first. Rothman has also argued that causes have to occur before outcomes. This is a sine qua non of any causal

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INTRODUCTION TO EPIDEMIOLOGIC RESEARCH METHODS

relationship and so any consideration of cause has to include this criterion. Rothman [5] emphasises that causation implies a comparison. Smoking one pack of cigarettes a day is not a cause if it is compared to two packs, but is a cause when compared to a person who smokes no cigarettes. This comparison is usually measured in epidemiology by calculating an index of association, such as an odds ratio, between a possible causal factor and the disease or outcome of interest. For example, smoking cannabis regularly doubles the risk of schizophrenia compared to people who do not smoke cannabis [12] (though whether this is a causal relationship is still uncertain). In everyday talk, people often think of causes as though they have a one-to-one relationship with an outcome. The smashed china was caused by the ball kicked by your son. This approach is also attuned to the deterministic model common in basic science, in which, for example, a neurotransmitter acts on a receptor, that is coupled with a G protein that in turn activates a signal transduction pathway. However, the model of causation in clinical medicine has increasingly regarded causes as neither necessary nor sufficient for the majority of non-infectious medical conditions. Smoking cigarettes increases the risk of lung cancer, but many people who smoke do not develop lung cancer and some people develop lung cancer without smoking. It is possible to think of some exceptions to this rule, but in the main these are single gene disorders with high penetrance such as Huntington’s disease. In infectious disease, the infectious agent is necessary, but not always sufficient for the clinical disease. Nevertheless, for most non-infectious disease, there has grown a consensus that causal factors are likely to be neither necessary nor sufficient. This has also encouraged use of the term ‘risk factor’ in epidemiology as the causal factors that are identified in human populations increase the risk of disease but do not confer any certainty about future events. At first sight there appears to be a conflict between the deterministic models used in biological science and the more probabilistic models that seem to apply to disease in human populations. There are two ways in which this apparent conflict has been resolved. First, that most diseases have multiple causes and this would seem particularly true for psychiatric

disorder. The evidence from heart disease and cancer provides ample evidence that this can be the case. The other suggestion, again made by Rothman [13], is the idea of multiple sufficient causes for a single disease, and that each of these sufficient causes are in turn multifactorial and with overlapping sets of causal factors. If we accept this model, it is possible to understand that in a circumstance of partial knowledge, each element of those sufficient causes will appear neither necessary nor sufficient. This is an important argument that enables us to link epidemiology to the underlying mechanisms that underpin the associations that epidemiologists will observe in human populations.

1.2.1 Alternative explanations Epidemiological studies estimate the association between a possible causal factor and a disease or a treatment and recovery. In human populations, this is the only approach that is feasible. We also have to understand that the tight experimental controls that can occur in basic science and in experimental animals are impossible in epidemiological studies of human populations. Participants in epidemiological studies or clinical trials will change their behaviour, change their treatment, and may refuse to continue to take part in a study. On occasions, these changes will be influenced by the study itself, public health campaigns or changes to health policy. There will always be difficulties therefore, in interpreting data from epidemiological studies. There are no perfect studies in epidemiology and this leads to more emphasis upon interpretation of any finding of association. It also implies that single studies are rarely sufficient, on their own, to draw conclusions. It is common for RCTs to be described as the ‘gold standard’ but this ignores the difficulties in interpreting even that most rigorous of the designs at our availability. Patients drop out of RCTs, stop taking their medication, start taking non-trial medication or make other changes to their lifestyle and health care use, sometimes as a result of the randomised intervention. RCTs might reduce the controversy surrounding interventions but they do not eliminate them [14, 15]. If this is epidemiological gold, it has less lustre than its counterpart in government vaults. 3

CHAPTER 1

One approach towards causal inference is therefore to consider the alternative explanations for an association, apart from causation and it is usual to consider at least these four alternatives: sampling variation and chance, confounding, bias and reverse causality.

1.2.1.1 Sampling variation and chance Epidemiologists have been at the forefront of considering statistical issues in relation to medical research. There is marked variation within human populations and so sampling variation is usually important to consider. It is difficult to imagine the days when medical journals did not include any statistical tests, but at least in the United Kingdom, Bradford Hill’s series of articles in The Lancet in the 1930s were very influential in introducing statistical tests into medicine [16]. Many studies are completed and many statistical tests are carried out, even within a single study. Every article in a scientific journal will usually contain dozens of statistical tests. Type 1 errors in which results are statistically significant by chance are therefore common. Statistical tests can be very useful when an analysis was planned as part of a hypothesis driven investigation. However, carrying out repeated tests during exploratory analyses or ‘data mining’ can lead to results that will often be due to chance. Results from exploratory analyses are best thought of as ‘hypothesis generating’ that require replication. It is particularly difficult when unscrupulous investigators report such analyses as though they were testing a priori hypotheses. In the light of these concerns, the conventional 5% threshold for statistical significance is almost certainly too high [17], and for most decisions, one needs much better statistical evidence. Type 2 errors, in which non-significant findings are interpreted as reflecting no association, are very common in the psychiatric literature given the relatively small size of many studies. Confidence intervals can help you decide upon the accuracy with which an association is estimated and help to decide if the investigators have excluded an important result. This is a common circumstance in treatment research in psychiatry [18].

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1.2.1.2 Confounding Factors of aetiological importance are not randomly allocated in human populations. In RCTs of sufficient size there should be a complete balance between the groups in confounding factors, including those that the investigator does not know about. In observational studies, however, confounding can occur. For example, cannabis users will differ in many ways from people who do not use cannabis. In the Swedish conscript study, cannabis users were more likely to live in cities, were more sociable and were more likely to get into trouble with the police [19]. It is possible that these other characteristics could alter risk of subsequent psychosis. These ‘other characteristics’ are potential confounding variables. A confounder is defined as an independent risk factor (or protective factor) for the outcome at each level of the exposure, that is also associated with the exposure. A confounding factor can lead to a spurious association or can eliminate a real association between exposure and disease. In the case of cannabis and psychosis, there is good evidence that confounding occurs [12]. In other words, much of the increased risk of psychosis in cannabis users can be attributed to their other characteristics. Statistical adjustment for confounders accounted for about half, but only half, of the observed association.

1.2.1.3 Bias Bias is another epidemiological term that is borrowed from normal every day use. In epidemiology, bias refers to the possibility that the estimate of association that is obtained is not the ‘true’ association that would pertain if one could carry out a perfect study. It can be contrasted with confounding, that is, a real explanation for an association that would be present even if your study had perfectly estimated the association in the population. In contrast, bias is introduced by the investigator or is a consequence of the investigation. The distinction between confounding and bias can be illustrated using the example given above of the link between cannabis and schizophrenia. Even if the measurement of cannabis and schizophrenia were

INTRODUCTION TO EPIDEMIOLOGIC RESEARCH METHODS

done perfectly and everyone in a study was followed up, confounding would still exist and have to be considered. Bias will only be introduced as one departs from this utopian state. There are two main types of bias: selection and measurement bias. Selection bias is to do with the selection of subjects for the study while measurement or information bias is concerned with bias in measurement, diagnosis and ascertainment of outcome and confounders. There are more comprehensive classifications of bias [7], but in the main these two types are the most important to consider. Selection bias is often described in relation to case–control studies that are very susceptible to this bias. It occurs when the cases and controls in a case–control study are drawn from different populations that differ with respect to the exposure variable. In case–control studies, controls estimate the frequency of exposure in the population from which the cases were drawn. If the control were to become diseased the control should be in the sampling frame for the cases. Case–control studies are therefore population based studies and it is this aspect of case–control design, that is often overlooked. For example, Mulvany and colleagues [20] carried out a case–control study in which people with schizophrenia (the cases) were selected from a hospital in Dublin who had birth records in the local maternity hospitals. The controls were the next birth in that hospital. There was no way of knowing whether the controls were still resident in Dublin when adult so might not have been in the population ‘at risk’ of being cases in the study. Some of the controls will have moved away from Dublin. This mismatch could lead to selection bias. This study reported that people of higher socioeconomic status were more likely to develop schizophrenia but this might have been because wealthier people were less likely to move away between birth and adulthood. This result is the opposite of the findings from a cohort study [21] and a case–control study with less risk of selection bias [22] that both found that people of lower socioeconomic status were at increased risk of schizophrenia. On balance, the Mulvany study does not support the idea that higher social classes

are at risk of developing schizophrenia; if anything, the reverse is the case. Selection bias can also be used to describe the bias introduced by partial follow-up in cohort studies and RCTs. Cohort studies are relatively insensitive to the selection of participants in the cohort, for example the British doctors’ cohort of Doll and Hill [23] has produced some robust and reproducible findings even though British doctors are a highly selected group. Likewise, Framingham is far from a representative town. However, bias is more likely to be introduced by differential drop out from the cohort than from the initial selection of the subjects in the cohort, at least in this kind of design. Many cohort studies have quite marked attrition, particularly for longer term follow-up and statistical methods for dealing with such missing data (see www.missingdata.org.uk) are designed to reduce this form of bias. Measurement or information bias occurs when measurement of exposure or ascertainment of disease is influenced by knowledge of the exposure (longitudinal designs or cross-sectional designs) or of the outcome (case–control and cross-sectional designs). Recall bias can be a problem if the presence of disease influences the measurement of exposure, as might occur in case-control studies and cross-sectional surveys. People with an illness, or their relatives, are likely to be more aware of past events that might be relevant to illness. The mental state of people with psychiatric disorder might increase or reduce the chance that past events are remembered. For example, people with depression have well-documented information processing biases that make it more likely that negative events are recalled [24]. There are many examples of studies that ask people with depression to record negative adverse experiences [25]. The strong associations that have been observed between depression and these measures may be partly as a result of such a recall bias. It is always difficult or impossible to estimate the likely influence of bias on results. The high chance of recall bias when measuring factors of potential aetiological importance in psychiatry is a powerful argument for using longitudinal designs to study causation. Using data sources gathered before the onset of disease will

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also reduce measurement bias. Other strategies to reduce measurement bias include using structured questionnaires and restricting retrospective inquiry to events that are unlikely to be forgotten. Bias can also be introduced by the researcher who is interviewing the participant, so-called observer bias. If possible, this source of bias can be eliminated by using self-administered questionnaires. However, there are occasions when participants might find the questions in self-administered form difficult to understand or when they might be misinterpreted. This seems particularly likely when asking about psychotic symptoms [26]. Many assessments of psychiatric disorder are semistructured and rely upon ‘cross-examination’ of the participant. There has been a vigorous debate comparing the validity and reliability of self-reported and semistructured interviews in assessing psychiatric disorder [27]. One has to balance the danger that questions can be misinterpreted with the risk that the observer can influence findings according to preconceived views. The balance of these arguments differs according to the diagnoses that are being studied. For most depression and anxiety disorders where insight is retained, self-reported information would seem to be an advantage. In contrast, for psychotic disorders the cross-examination style of semistructured interviews would seem necessary.

1.2.1.4 Reverse causality Finally, the disease may cause the exposure. This might occur in case–control studies and crosssectional surveys because data on exposure is usually collected retrospectively. In contrast, longitudinal studies should ensure that exposures occur before the onset of disease. Many biological aspects of psychiatric disorder are studied using case–control methods. For example, in imaging studies the abnormalities described in people with schizophrenia could result from the illness rather than being a marker of possible causes. Studies of first episode psychosis [28] go some way to address this possibility, but longitudinal studies are required in order to establish abnormalities that are present before the onset of psychosis.

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1.3 Causal inference A number of criteria have been suggested that might encourage a conclusion that exposures have a causal role in disease [13, 29, 30]. These usually require evidence from a variety of sources and one would expect a number of different studies using different approaches all to produce consistent results before coming to a conclusion about causality. The criteria usually suggested include: 1 Timing. The cause has to occur before the disease. 2 Strength of relationship measured by relative risk. Large relative risks are more likely to be causal. A relative risk below about 1.5 should be treated with more caution. 3 Consistency of findings across studies. One would want a variety of different studies in different populations and with different strengths and weaknesses in the design all to produce the same results. 4 Dose–response relation. Does the evidence support a ‘dose–response’ relation in that the more exposure to a risk factor the more likely the disease. 5 Biological plausibility. Is the relationship biologically plausible and underpinned by a reasonable mechanism? One advantage of epidemiology is that it can work in isolation of knowledge of mechanisms. For example, John Snow argued that contaminated water led to cholera many decades before the cholera Vibrio was identified or the molecular basis of that disease was established. This should be especially useful for psychiatric epidemiology given the complexity of brain structure and function and the limits of our basic neuroscientific knowledge. None of the criteria listed above are essential, except perhaps for the issue of timing – causes have to occur before the onset of disease. These criteria are a guide, but often the final conclusion relies upon a matter of judgement. One important principle to consider is whether the evidence is good enough to justify any policy decisions that might be taken. For example, if cannabis

INTRODUCTION TO EPIDEMIOLOGIC RESEARCH METHODS

had a causal relationship to schizophrenia then the main policy implication would be to carry out a public health campaign to alert young people to the possible dangers. The amount of evidence required to justify this would be less than that needed to justify a more expensive or risky intervention. For example, suggestions to recommend widespread use of cholesterol-lowering agents has to take account of the greater financial cost and potential for adverse effects. The strength of evidence required for such an intervention would be greater than that needed for a publicity campaign.

1.4 The future for psychiatric epidemiology Studying the causes of psychiatric disorder in human populations has to be carried out using epidemiological methods. Basic science experiments can often suggest likely causal mechanisms and generate hypotheses about the risk factors for psychiatric disorder but cannot support that such mechanisms are operating in humans. Small-scale experimental studies in humans can illustrate if these mechanisms are occurring in humans with disease but they cannot argue if they are causing the disease in human populations. For example, the work of Meaney and others [31] has suggested possible influences on stress reactivity based upon work on experimental animals. Small-scale experimental work on humans can investigate possible mechanisms further. However, it is only by studying humans in population-based studies that allow us to infer whether the kind of stresses that exist in human life could lead to permanent changes in hypothalamo–pituitary–adrenal axis responsivity and thus lead to human disease. The future of psychiatric epidemiology will rest upon advances in neuroscience and will increasingly need to measure psychological and biological processes in population based studies. Likewise, epidemiology can generate hypotheses that will need to be investigated by basic scientists and in smaller scale experimental studies in humans. This approach is often described as ‘translational medicine’ [32] and epidemiology will remain one of its key building

blocks if this vision is to be realised and the benefits of medical research to human health will be achieved.

References [1] Last, J. (2001) A Dictionary of Epidemiology, 4th edn, Oxford University Press, New York. [2] Rothman, K. and Greenland, S. (1998) Modern Epidemiology, 2nd edn, Lippincott, Williams & Wilkins, Philadelphia. [3] Snow, J. (1936) On the Mode of Communication of Cholera, 2nd edn, The Commonwealth Fund, New York. [4] Shepherd, M. (1978) Epidemiology and clinical psychiatry. Br. J. Psychiatry, 133, 289–298. [5] Rothman, K. (1987) Modern Epidemiology, Little Brown, Boston. [6] Morris, J.N. (1975) Uses of Epidemiology, 3rd edn, Churchill Livingstone, Edinburgh. [7] Sackett, D.L. and Holland, W.W. (1975) Controversy in the detection of disease. Lancet, 2 (7930), 357–359. [8] Evidence-Based Medicine Working Group (1992) Evidence-based medicine. a new approach to teaching the practice of medicine. J. Am. Med. Assoc., 268 (17), 2420–2425. [9] Tanskanen, P., Ridler, K., Murray, G.K. et al. (2008) Morphometric brain abnormalities in schizophrenia in a population-based sample: relationship to duration of illness. Schizophr. Bull., 36, 766–777. [10] Strickland, P.L., Deakin, W.J.F., Percival, C. et al. (2002) Bio-social origins of depression in the community. Br. J. Psychiatry, 180, 168–173. [11] Putnam, R.D. (1993) The prosperous community: social capital and public life. Am. Prospect, 13, 35–42. [12] Moore, T., Zammit, S., Lingford-Hughes, A. et al. (2007) Systematic review of cannabis use and risk of developing psychotic or affective outcomes. Lancet, 370, 319–328. [13] Rothman, K.J. and Greenland, S. (2005) Causation and causal inference in epidemiology. Am. J. Public Health, 95 (Suppl. 1), S144–S150. [14] Gotszche, P.C. and Olsen, O. (2000) Is screening for breast cancer with mammography justifiable? Lancet, 355, 129–134. [15] Marshall, M. and Creed, F. (2000) Assertive community treatment – is it the future of community care in the UK? Int. Rev. Psychiatry, 12, 191–196. [16] Doll, R. (1992) Sir Austin Bradford Hill and the progress of medical science. Br. Med. J., 305 (19–26), 1521–1526.

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CHAPTER 1 [17] Sterne, J.A. and Davey, S.G. (2001) Sifting the evidence – what’s wrong with significance tests? Br. Med. J., 322 (7280), 226–231. [18] Hotopf, M., Lewis, G. and Normand, C. (1997) Putting trials on trial: the costs and consequences of small trials in depression. J. Epidemiol. Community Health, 51, 354–358. [19] Zammitt, S., Allebeck, A., Dalman, C. et al. (2002) Self-reported cannabis use as a risk factor for schizophrenia: further analysis of the 1969 Swedish conscript cohort. Br. Med. J., 325, 1199–1201. [20] Mulvany, F., O’Callaghan, E., Takei, N. et al. (2001) Effect of social class at birth on risk and presentation of schizophrenia: case–control study. Br. Med. J., 323 (7326), 1398–1401. [21] Wicks, S., Hjern, A., Gunnell, D. et al. (2005) Social adversity in childhood and the risk of developing psychosis: a national cohort study. Am. J. Psychiatry, 162 (9), 1652–1657. [22] Harrison, G., Gunnell, D., Glazebrook, C. et al. (2001) Association between schizophrenia and social inequality at birth: case–control study. Br. J. Psychiatry, 179, 346–350. [23] Doll, R., Peto, R., Boreham, J. et al. (2000) Smoking and dementia in male British doctors: prospective study. Br. Med. J., 320 (7242), 1097–1102. [24] Mathews, A. and MacLeod, C. (2005) Cognitive vulnerability to emotional disorders. Annu. Rev. Clin. Psychol., 1, 167–195.

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[25] Paykel ES. (2001) The evolution of life events research in psychiatry. J. Affect. Disord., 62 (3), 141–149. [26] Horwood, J., Salvi, G., Thomas, K. et al. (2008) IQ and non-clinical psychotic symptoms in 12-year-olds: results from the ALSPAC birth cohort. Br. J. Psychiatry, 193 (3), 185–191. [27] Wittchen, H.U., Ustun, T.B. and Kessler, R.C. (1999) Diagnosing mental disorders in the community. A difference that matters? Psychol. Med., 29 (5), 1021–1027. [28] Steen, R.G., Mull, C., McClure, R. et al. (2006) Brain volume in first-episode schizophrenia: systematic review and meta-analysis of magnetic resonance imaging studies. Br. J. Psychiatry, 188, 510–518. [29] Hill, A.B. (1965) The environment and disease: association or causation? J. R. Soc. Med., 58, 295–300. [30] Susser, M. (1991) What is a cause and how do we know one? A grammar for pragmatic epidemiology. Am. J. Epidemiol., 133 (7), 635–648. [31] Meaney, M.J. (2001) Maternal care, gene expression, and the transmission of individual differences in stress reactivity across generations. Annu. Rev. Neurosci., 24, 1161–1192. [32] Sung, N.S., Crowley, W.F.Jr., Genel, M. et al. (2003) Central challenges facing the national clinical research enterprise. J. Am. Med. Assoc., 289 (10), 1278–1287.

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Analysis of categorical data: The odds ratio as a measure of association and beyond Garrett M. Fitzmaurice1,2,3 and Caitlin Ravichandran1,2 1 Laboratory

for Psychiatric Biostatistics, McLean Hospital, Belmont, MA, USA Department of Psychiatry, Harvard Medical School, Boston, MA, USA 3 Department of Biostatistics, Harvard School of Public Health, Boston, MA, USA 2

2.1 Introduction In this chapter we present an overview of many of the statistical methods commonly used for the analysis of categorical ‘outcome’ data in psychiatric studies. A categorical variable is defined as one that takes on a finite number of levels or categories (e.g. ‘success’ and ‘failure’ in the case of a dichotomous or binary variable). For example, consider the data in Table 2.1 which are from a study of rates and predictors of recovery in patients with first-episode major affective disorders with psychosis [1]. In this study investigators obtained information on candidate predictors of recovery at the time of first hospitalisation (e.g. Axis I comorbidity) and then followed patients for 2 years to determine which patients experienced syndromal and functional recovery. In this simple illustration of one comparison of interest, the categorical outcome has two levels, ‘recovered’ or ‘not recovered’. Table 2.1 is commonly referred to as a 2 × 2 contingency table. Much of the statistical theory underlying the analysis of categorical data is more easily formulated for 2 × 2 contingency tables. Indeed, methods for the analysis of 2 × 2 contingency tables provide the cornerstone for many of the advanced statistical methods required for more complicated problems. These include

Table 2.1 Illustrative data from a study of recovery in patients with first-episode major affective disorders with psychosis. Comorbidity

No Axis I Axis I Total

Recovery

Total

Not recovered

Recovered

65 48 113

50 18 68

115 66 181

extensions for analysing outcomes with more than two levels (e.g. ‘not recovered’, ‘partially recovered’ and ‘recovered’), which may or may not be ordered; the former are referred to as ordinal variables, the latter are referred to as nominal variables. In addition, there can be more than two levels of the experimental treatment or exposure variable (e.g. no Axis I comorbidity, one Axis I comorbidity, two or more Axis I comorbidities) and other factors or covariates (e.g. age, gender, health status before treatment) that influence the outcome variable. Some of the most widely used probability distributions for categorical outcomes include the Bernoulli, binomial, hypergeometric and multinomial distributions. Throughout this chapter we assume the reader has very little prior knowledge of these probability distributions. The chapter is

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

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organised as follows. We begin with a discussion of inference for a single probability or proportion. This is followed by a description of methods for analysing 2 × 2 contingency tables; the extensions to R × C contingency tables (i.e. contingency tables with R rows and C columns) are mentioned but not discussed in great detail. We discuss measures of association for 2 × 2 tables that quantify departures from independence. In particular, we focus on the odds ratio (OR) as a measure of association. We also discuss the analysis of sets of 2 × 2 tables, and describe the Cochran–Mantel–Haenszel test. Finally, we present an overview of regression models for categorical data, focusing extensively on logistic regression models for binary outcomes. The logistic regression model is first introduced for the simple case where there is only a single predictor or covariate. This model is compared and contrasted with the classical linear regression model. Later the generalisations to more than one predictor variable are considered. A major emphasis of this chapter is placed on how logistic regression is used in practice and how the logistic regression coefficients should be interpreted. An example, based on data from the first-episode major affective disorders with psychosis study, is used to illustrate and reinforce the main concepts. Finally, at the end of the chapter, we introduce some advanced topics, including extensions of logistic regression to matched study designs; exact logistic regression, which is appropriate for small sample sizes or sparse data; multinomial regression models for nominal and ordinal outcomes; and applications of logistic regression models to so-called ‘clustered’ categorical data, when the outcomes are not independent.

2.2 Inference for a single proportion In this section we discuss inference for a single proportion or probability. In order to motivate the methods, we consider data from the first-episode major affective disorders with psychosis study. One of the goals of this study was to estimate the probability that patients with first-episode major affective disorders with psychosis achieve functional recovery after 2 years. The outcome for each patient can 10

be denoted ⎧ ⎪ ⎨ 1 Yi = ⎪ ⎩ 0

if the patient achieves functional recovery, if the patient does not achieve functional recovery

for i = 1, . . . , n patients. The binary outcomes for the n patients are assumed to be independent of each other. The probability of success (e.g. ‘recovered’) is denoted by p = pr(Yi = 1) and the probability of failure (e.g. ‘not recovered’) by 1 − p = pr(Yi = 0). The distribution of the number of successes among  the n patients, Y = ni=1 Yi can be used to form test statistics and a confidence interval for p. Counts of the number of successes, Y, have a binomial probability distribution   n y pr(Y = y) = p (1 − p)n−y , y   n where the binomial coefficient, , is the number y of ways y ‘successes’ can be obtained in n trials. The probability of success can be estimated using the sample proportion of successes, p = Yn . In large samples (say, n > 30, and with the expected number of successes np ≥ 5 and the expected number of failures n(1 − p) ≥ 5), p has an approximate normal distribution with mean p and variance p(1−p) n . A 95% confidence interval for p is given by

p(1 − p) p ± 1.96 . n The above confidence interval for p, known as a Wald confidence interval, is commonly used and easy to compute, but has been criticised for its poor performance; for example these confidence limits cover the true value of p less than 95% of the time on average. Two alternatives with more favourable properties are the Wilson confidence interval, which is based on the score test, and the Jeffreys interval, which can be derived using Bayesian statistical theory. Both can be calculated using popular statistical software, and the Wilson interval also has the closed-form expression:  z21−α/2 p(1 2 ˆ ˆ − p) +

z1−α/2 4n pˆ + ± z1−α/2 2n n , (2.1) z21−α/2 1+ n

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

where z1−α/2 = 1.96 for a 95% confidence interval. For more information on the performance of these and other intervals, see for example Brown, Cai and DasGupta [2]. When sample sizes are relatively small (say, n < 30), an exact confidence interval can be obtained that is based directly on the binomial distribution for Y. Finally, hypothesis tests for p equalling a specified value, say po , can be conducted using either large sample theory for the approximate normal distribution of p or via exact methods based on the binomial distribution for Y.

2.2.1 Example Using data from the first-episode major affective disorders with psychosis study presented in Table 2.1 and the methods for inference for a single proportion, we can estimate the proportion of patients who achieve functional recovery 2 years after first hospitalisation. The estimated proportion is the total number of patients who recovered (Y = 68) divided by the total number of patients (n = 181), which equals 0.376. Ninety-five per cent confidence intervals for this estimate are (i) Wald: (0.305, 0.446), (ii) Wilson: (0.308, 0.448), (iii) Jeffreys: (0.308, 0.448) and (iv) exact: (0.305, 0.451). Note that there is close agreement among the four confidence intervals; this is to be expected when, as with these data, n is relatively large and both n p ≥ 5 and n(1 − p) ≥ 5.

2.3 Analysis of 2 × 2 contingency tables In many settings we are interested in the effect of treatments or exposures on a binary outcome. When the treatment or exposure has only two levels the data can be summarised in a 2 × 2 contingency table. Data in the form of a 2 × 2 contingency table can arise from many different types of study designs [3]. For example, consider a clinical trial comparing the probability of remission between patients with depression assigned to a novel treatment or standard treatment. The question of scientific interest is: ‘How does treatment affect the probability of remission?’ Similarly, for the first-episode major affective disorders with psychosis study (Table 2.1), the presence of Axis I comorbidities (the exposure) was determined

at baseline, and we are interested in the number of patients with and without Axis I comorbidities who recover. The question of scientific interest is: ‘How does the presence of comorbidities affect recovery?’ Both are examples of prospective study designs. However, data in the form of 2 × 2 tables also arise from other types of study designs. Consider, for example, the data from a retrospective case–control study of psychiatric disorders and occurrence of elderly suicides [4] presented in Table 2.2. The number of suicide cases and controls (non-cases) are fixed by design (with 85 cases and 153 controls) and the prevalence of psychiatric disorders is then ascertained on each subject in the study. In this retrospective case–control study design, the prevalence of psychiatric disorder is considered a random variable. Case–control studies are commonly used when the outcome is rare and/or when it is not ethical to randomise patients to the ‘exposure’ in a prospective study. In this particular case–control study one question of scientific interest is: ‘Does prevalence of substance use disorders vary among the cases and controls?’ The third type of study design in which data in the form of a 2 × 2 table arise is the so-called double dichotomy, cross-sectional or prevalence study. In this study design a fixed number (n) of subjects are randomly selected and each subject is crossclassified on the basis of the two variables (the row and column variables) of scientific interest. Table 2.3 displays data from a prevalence study of neuropsychiatric symptoms and mild cognitive impairment (MCI) in the elderly [5], where only the total number of subjects, n = 1969, is fixed by design. Table 2.3 contains data on the presence of delusions for the 1909 subjects with neuropsychiatric data available. In this example, the question of scientific interest is: ‘Are delusions and cognitive status related?’

Table 2.2 Substance use disorders (SUDs) and occurrence of elderly suicides. SUD

Yes No Total

Status

Total

Case

Control

23 62 85

1 152 153

24 214 238

11

CHAPTER 2 Table 2.3 Data from the study of neuropsychiatric symptoms and MCI. Delusions

Yes No Total

Cognitive status MCI

Normal cognitive ageing

11 308 319

6 1584 1590

Total

17 1892 1909

Finally, although not shown here, data in the form of a 2 × 2 table can arise when the total sample size, n, is not fixed in advance. For example, an exit poll conducted at an election station might set out to record the political party preferences (e.g. Democrat or Republican) and opinions about mental health parity legislation (in favour or against) of all respondents who agree to participate in the poll; here, the total number of individuals who agree to participate, n, is random. Suppose we let Xi denote the row variable (e.g. treatment or exposure) and Yi denote the column variable (e.g. outcome variable) for each one of these types of study designs, where both Xi and Yi are binary (taking values 0 or 1). Then, the data in a general 2 × 2 contingency table can be represented as in Table 2.4. In Table 2.4 njk is the count of the number of subjects with X = j and Y = k; njk is referred to as a cell count. For example, n11 is the number of subjects with X = 1 and Y = 1. Also, in Table 2.4 the marginal row counts are nj+ = nj0 + nj1 (the

Table 2.4 General representation of counts in a 2 × 2 contingency table. Y 0 1 Total

0

n00

n01

Table 2.5 Probabilities in a 2 × 2 contingency table, with only n fixed.

Y

n0+

X

12

number of subjects with X = j), and the marginal column counts are n+k = n0k + n1k (number of subjects with Y = k). In each study, different marginal totals are fixed by design. As a result, the counts in the tables have different distributions. For example, for the case–control study, n+0 and n+1 are fixed by design, and the numbers of exposed subjects in each column (n10 and n01 ) have independent binomial distributions. However, for all of these different types of study designs, the question of scientific interest can be formulated in a similar way: ‘Are X and Y associated or are they independent?’ For ease of explanation, we focus on data arising from a cross-sectional study design. For the cross-sectional design, we can write the probabilities for the 2 × 2 table as in Table 2.5. The probabilities in Table 2.5 are pjk = pr[(Xi = j), (Yi = k)], and the marginal probabilities are pj+ = pj0 + pj1 = pr[X = j] and p+k = p0k + p1k = pr[Y = k]. For the cross-sectional design, all of these probabilities can be estimated from the data at hand. For prospective studies with the number of exposures fixed by design, and for case-control studies, they are not all estimable. For prospective studies with the number of exposures fixed by design, only the two conditional row probabilities pr(Yi = 1|Xi = 0) = p01 /p0+ and pr(Yi = 1|Xi = 1) = p11 /p1+ can be estimated. Similarly, for case–control studies, only the two conditional column probabilities pr(Xi = 1|Yi = 0) = p10 /p+0 and pr(Xi = 1|Yi = 1) = p11 /p+1 can be estimated. For example, using data from the study

0

1

Total

0

p00

p01

p0+

X 1

n10

n11

n1+

1

p10

p11

p1+

Total

n+ 0

n+1

n

Total

p+0

p+1

1

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

of psychiatric disorders and occurrence of elderly suicides, the probability of a substance use diagnosis can be estimated for suicides and non-suicides, but the probability of suicide cannot be estimated for elderly with and without substance use diagnoses.

That is, the OR for Y associated with X is equal to the OR for X associated with Y, pr(Yi = 1|Xi = 1)  pr(Yi = 1|Xi = 0) OR = pr(Yi = 0|Xi = 1) pr(Yi = 0|Xi = 0) pr(Xi = 1|Yi = 1)  pr(Xi = 1|Yi = 0) = . pr(Xi = 0|Yi = 1) pr(Xi = 0|Yi = 0)

2.3.1 The odds ratio as a measure of association

It is this property, unique to the OR, that accounts for its widespread use for assessing the association between exposure and disease in case–control studies. In addition, in ‘rare disease’ settings, the OR is a close approximation to another measure of association called the relative risk (RR). The RR is defined as pr(Yi = 1|Xi = 1) RR = , pr(Yi = 1|Xi = 0)

To determine whether Xi and Yi are associated, it becomes necessary to formulate measures of association that quantify any departure from independence. The most commonly used measure of association is the odds ratio (OR), also known as the cross-product ratio (for reasons that will soon become apparent). The OR is a measure of association based on a comparison of ‘odds’. The odds is simply another metric for expressing risk or probability. Specifically, if p is p the probability of success, then 1−p is referred to as the odds of success. For example, if the probability of success is 0.8 then the odds of success is 4 (or 0.8 0.2 ) to 1. That is, the probability of success is four times as large as the probability of failure. In a prospective study with the number of exposures fixed by design, the OR measures association by comparing the odds of Y in the two exposure groups defined by X. Specifically, the OR for Y associated with X is OR =

pr(Yi = 1|Xi = 1)  pr(Yi = 1|Xi = 0) . pr(Yi = 0|Xi = 1) pr(Yi = 0|Xi = 0)

The null value for the OR is 1 because it corresponds to pr(Yi = 1|Xi = 1) = pr(Yi = 1|Xi = 0) and implies that Y and X are independent. Quite often, the log of the OR is used as a measure of association, since log(OR) = 0 under the assumption of no association between Y and X. When OR > 1, then pr(Yi = 1|Xi = 1) > pr (Yi = 1|Xi = 0); similarly, when OR < 1, then pr(Yi = 1|Xi = 1) < pr(Yi = 1|Xi = 0). Note that the OR expresses association in relative (or multiplicative) terms in the sense that the odds of success in one group (e.g. unexposed group) is multiplied by OR to obtain the corresponding odds in the other group (e.g. exposed group). An appealing property of the OR is that it is symmetric in the roles of Y and X in the sense that reversing the roles of Y and X yields the same OR.

and also expresses association in relative or multiplicative terms. Unlike the OR, however, the RR is not symmetric in Y and X. The relationship between the OR and the RR will be discussed in greater detail in Section 2.5.1. Finally, we note that a simple computational formula for the OR arises from the following equivalent expression, OR =

p00 p11 . p10 p01

This expression helps to explain why the OR is sometimes referred to as the ‘cross-product ratio’. It is usually of interest to obtain a point estimate and confidence interval for the OR, and to test the null hypothesis that the OR equals 1. For all four designs, the OR can be estimated as  = n00 n11 . OR (2.2) n10 n01  is approximately normally disBecause the log(OR) tributed, and because it will always result in nonnegative estimates of the OR, it is preferable to obtain a confidence interval for log(OR), and then exponentiate the endpoints. That is, a 95% confidence interval for log(OR) is given by   ± 1.96 Var[log(   log(OR) OR)], (2.3)   = 1 + 1 + 1 + 1 . Then, where Var[log( OR)] n00 n10 n01 n11 a 95% confidence interval for the OR is obtained by exponentiating the endpoints of this interval,     ± 1.96 Var[log(   exp log(OR) OR)] .

13

CHAPTER 2

Finally, suppose it is of interest to construct a test for no association (independence). There are three commonly used test statistics. The Wald test statistic for the null hypothesis, H0 : log(OR) = 0, is given by: Z= 

 log(OR)   Var(log( OR))

,

(2.4)

which, in large samples, has an approximate standard normal distribution, denoted by N(0, 1), under the null hypothesis of no association. Alternatively, the likelihood ratio test (LRT) statistic can be used. This is simply twice the difference in the log-likelihood under the alternative (association) and null (independence) hypotheses. Remarkably, for any of the four types of study designs considered, the LRT statistic reduces to G2 = 2

1  1 

 Ojk log

j=0 k=0

Ojk Ejk

 ,

(2.5)

where Ojk = njk is the ‘observed’ count in the 2 × 2 table and Ejk = E(njk |H0 ) = nj+ n+k /n is the ‘estimated expected’ count (under the assumption of independence). In addition, for any of the four study designs, the score test statistic reduces to X2 =

1  1  (Ojk − Ejk )2 j=0 k=0

Ejk

,

(2.6)

which is also known as the Pearson chi-square test for a 2 × 2 table. In large samples, both the likelihood ratio and the Pearson chi-square statistics have approximate chi-square distributions with 1 degree of freedom. Similarly, in large samples, the Wald test statistic has an approximate standard normal distribution or, equivalently, the squared Wald test statistic has an approximate chi-square distribution with 1 degree of freedom. If the sample size, n, is relatively small, these asymptotic (or very large sample) approximations cannot be relied upon. In particular, a rule-ofthumb in statistical folklore is that the asymptotic approximations cannot be relied upon if one (or say 25%) of the cells in the 2 × 2 table have estimated expected counts (Ejk ) less than 5. When at least

14

one Ejk is less than 5, and it is of interest to make inferences about the OR, a common technique is to fix both margins of the 2 × 2 table and use so-called ‘exact’ tests and confidence intervals. That is, for a prospective study (where the row margins are fixed), we further condition on the column margins; for a case–control study (where the column margins are fixed), we further condition on the row margins; or for a cross-sectional design (where n is fixed), we condition on both row and column margins. In all of these cases it can be shown that the counts in the resulting table with fixed margins have a non-central hypergeometric distribution. Under the null hypothesis H0 : OR = 1, the non-central hypergeometric distribution becomes a central hypergeometric distribution, which forms the basis of Fisher’s exact test of no association in a 2 × 2 contingency table (see, for example [6]). This test is appropriate in small samples; the non-central hypergeometric can also be used to obtain an estimate of the OR that has better small sample properties than the usual OR estimate given in Equation 2.2. One potential drawback with exact methods, however, is that they can be ‘conservative’ in the sense that the true significance level of an exact test is often far smaller than the nominal level (e.g. 0.05), thereby making it more difficult to reject the null hypothesis of independence.

2.3.2 Examples Returning to the data from the first-episode major affective disorders with psychosis study in Table 2.1, the scientific interest is in the association between Axis I comorbidity and 2-year functional recovery. Using formulas from this section (Equations 2.2–2.6), the estimated OR comparing odds of recovery between patients with and without Axis I Comorbidity is 0.49, with 95% confidence interval (0.25, 0.94). We would estimate that patients with Axis I comorbidity have about one half the odds of 2-year functional recovery as patients without Axis I comorbidity. Performing a test of no association, we would obtain a Wald test statistic of Z = −2.15 with a p-value of 0.03, a LRT statistic of G2 = 4.81 with a p-value of 0.03, or a score (Pearson chi-square) test statistic of χ2 = 4.70 with

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

a p-value of 0.03. At the conventional α = 0.05 significance level, we would conclude there is a significant association between Axis I comorbidity and 2-year functional recovery among patients with first-episode major affective disorders with psychosis from any of these large-sample test statistics. For the data from the study of neuropsychiatric symptoms and MCI in Table 2.3, exact methods are more appropriate than large-sample methods due to small expected cell counts. For this example, the estimated OR comparing odds of MCI between elderly persons with and without delusions is 9.43, and the p-value for Fisher’s exact test is <0.001. We conclude that elderly persons with delusions have increased odds of MCI.

2.3.3 Analysis of R × C contingency tables In this section we briefly outline methods for the analysis of contingency table data when there are more than two rows and/or columns. Data often arise in the form of R × C contingency tables, where the number of rows R and/or the number of columns C is greater than 2. For example, in Table 2.2 substance use disorders could be divided into alcohol use disorder only and drug use disorders. In another example, using data from the first-episode major affective disorders with psychosis study, we may be interested in rates of 2-year functional recovery among patients with different types of onset. Suppose we again let Xi denote the row variable and Yi denote the column variable. The notation for an R × C table is a straightforward extension of the 2 × 2 table. In particular, let njk be the number of subjects with X = j and Y = k, and pjk = pr[(Xi = j), (Yi = k)], for j = 1, . . . , R and k = 1, . . . , C. For an R × C table, the question of scientific interest is once again: ‘Are X and Y associated or are they independent?’ To study departures from independence, it is possible to define sets of (R − 1)(C − 1) nonredundant ORs for an R × C table. For example, one such set of OR are those that are relative to the last row and column of the table, that is OR(j, R : k, C) =

pjk pRC , pjC pRk

(2.7)

for j = 1, . . . , R − 1, and k = 1, . . . , C − 1. The OR in Equation 2.7 is the OR conditional on rows j and R and columns k and C. If the rows and columns are independent, then all of these ORs equal 1. The estimate of this OR is  R : k, C) = OR(j,

njk nRC , njC nRk

and confidence intervals or hypothesis tests can be formed based on the large sample normality of the estimator of the log OR. Alternatively, the likelihood ratio or the Pearson chi-square tests can be used to test for independence of X and Y, and their form is identical to Equations 2.5 and 2.6, except that the sum is now over j = 1, . . . , R, and k = 1, . . . , C. If the sample size is relatively small (and at least 25% of the cells in the R × C table have estimated expected counts Ejk less than 5), then the asymptotic chi-square approximations for these test statistics cannot be relied upon. In that case Fisher’s exact test can be used to perform a test for no association in an R × C table. Finally, if the rows and columns are ordered, and scores are assigned to the rows and columns, the score test statistic for no association is simply a function of the correlation coefficient between the scores assigned to the rows and columns. On the other hand, if only one of the variables is ordered, and scores are assigned to the ordinal variable, then the score statistic is a function of the one-way analysis of variance (ANOVA) test statistic, where the ordinal variable is treated as the outcome, and the unordered variable is a factor or group variable. Both large sample (based on an asymptotic chi-square distribution) and exact p-values (based on the central hypergeometric) can be calculated for these score statistics.

2.3.4 Example The LRT or Pearson chi-square test can be used to test for independence between type of onset of firstepisode affective disorder with psychosis and 2-year functional recovery. For the data in Table 2.6, the LRT statistic is G2 = 0.29, and the Pearson chisquare statistic is χ2 = 0.29, both with p-values of 0.87. Either test provides no evidence of an

15

CHAPTER 2 Table 2.6 Additional data from the study of recovery in patients with first-episode major affective disorders with psychosis. Onset

Acute Subacute Chronic Total

Recovery

Total

Not recovered

Recovered

45 28 33 106

30 17 18 65

75 45 51 171

association between type of onset and two-year functional recovery.

2.4 Analysis of sets of 2 × 2 contingency tables When there are three or more categorical variables, we can form a ‘multidimensional contingency table’. In this setting all of the variables could be random, or some margins of the table could be fixed by design. One particular type of multidimensional contingency table results from a set of J 2 × 2 tables. For example, consider the data introduced earlier on the 181 patients with first-episode major affective disorders with psychosis (see Table 2.1). In Table 2.7 these patients are now cross-classified by sex (W), in addition to Axis I comorbidity (X), and recovery (Y). The 2 × 2 tables of (X, Y) at each level of W are referred to as partial or conditional tables; for example they express the relationship between comorbidity and recovery controlling for sex. The (Comorbidity, Recovery) table formed by combining (or collapsing over) the partial tables is referred to as the marginal table (Table 2.1). Similarly, the ORs in the partial tables are called partial odds ratios, and the OR in the marginal table is called the marginal odds ratio. When the ORs in the partial tables differ,

there is said to be interaction between W and (X, Y). On the other hand, when the partial ORs are the same, but the common partial OR is different from the marginal OR, there is said to be confounding. Confounding occurs when two variables are associated with a third in a way that obscures their relationship. In particular, W (Sex) can potentially confound the relationship between X (Comorbidity) and Y (Recovery) when W is related to both X and Y. In Table 2.7, there are two 2 × 2 tables. Suppose, in general, that there are J 2 × 2 tables, with notation as in Table 2.8. Let njk denote the number of subjects with (W = j, X = k, Y = ). Suppose it is of interest to test for no partial association, that is H0 : no association between Y and X given W = j, j = 1, . . . , J. For each of the 2 × 2 contingency tables, Cochran [7] and Mantel and Haenszel [8] proposed a test statistic based on conditioning upon both margins. Earlier, we discussed how this is valid for a single 2 × 2 table regardless of the type of study design; this result also generalises to J 2 × 2 tables. Thus, the following Cochran–Mantel–Haenszel test is valid for any design, including both prospective and case–control studies. Conditional on both margins of the jth table, the data follow a (central) hypergeometric distribution under the null hypothesis of no association, leading to the Cochran–Mantel–Haenszel test for H0 : no association between Y and X, given W, J Z=

Sex (W)

Male Female

16



J j=1

− Ej ]

,

Vj

Table 2.8 The jth 2 × 2 contingency table, j = 1, . . . , J.

Y 0

Table 2.7

j=1 [nj11

1

Total

Illustration of two 2 × 2 contingency tables. Comorbidity (X)

No Axis I Axis I No Axis I Axis I

0

nj00

nj01

nj0+

1

nj10

nj11

nj1+

Total

nj+0

nj+1

nj++

Recovery (Y) Not recovered

Recovered

35 31 30 17

27 10 23 8

X

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

where Ej =

nj1+ nj+1 nj++

is the mean of the hypergeo-

metric distribution and Vj =

nj1+ nj0+ nj+1 nj+0 n2 (n −1) j++ j++

is the

variance. The Cochran–Mantel–Haenszel statistic has an approximate N(0, 1) distribution under the null hypothesis provided that the number of tables is large, say J > 30, and/or the sample size in each table, nj++ , is large. An estimate of the adjusted OR is given by  (Adjusted) OR ⎛ ⎞ ⎛ ⎞ J J    =⎝ nj00 nj11 /nj++ ⎠ ⎝ nj01 nj10 /nj++ ⎠ . j=1

j=1

Among the available tests for interaction (homogeneity of the ORs) is the Breslow–Day test [3], which has an approximate chi-square distribution with (J − 1) degrees of freedom. Like the Cochran–Mantel–Haenszel test, this test is based on conditioning on both margins. However, unlike the Cochran–Mantel–Haenszel test, the Breslow–Day test requires that the sample size in each partial table is large even if the number of tables is large. The calculation of the Breslow–Day test statistic is more complex than other calculations presented in the chapter, but this test is readily available within most popular statistical software.

2.4.1 Example The Cochran–Mantel–Haenszel test statistic for the data in Table 2.7 for the test that the common OR equals one is Z = −2.12, with a p-value of 0.03; the estimate of the adjusted OR is 0.49 (with 95% confidence interval: 0.26, 0.95). From the Cochran–Mantel–Haenszel test and estimate of the adjusted OR, we conclude that, adjusting for sex, patients with Axis I comorbidity have significantly lower odds of recovery than patients without Axis I comorbidity. Finally, we note that the Breslow–Day test statistic for homogeneity of the ORs is χ21 = 0.32 with a p-value of 0.57. From the Breslow–Day test, we would conclude we have no evidence that the association between Axis I comorbidity and recovery differs between males and females (i.e. there is no interaction between comorbidity and sex).

2.4.2 Matched pair study design A matched pair study design is an example of a case when the number of partial tables (J) is large, and the sample size for each partial table (nj++ ) is small. The matched pair design has become increasingly popular in epidemiologic studies. In a matched case–control study, a case is selected, and then a control is matched to the case on factors that could be confounders of the association between the exposure and outcome variables. Then, as in the usual case–control study, investigators determine the exposure status (exposed, not exposed) of all subjects. For example, the data in Table 2.9, reported in Everitt [9], arose from a study designed to test the hypothesis that complications during pregnancy and birth, a known risk factor for the development of schizophrenia, are more prevalent in schizophrenics with a low age of onset (prior to age 16) compared to those with a later age of onset (after age 21). In this study, 36 subjects with low age of onset schizophrenia (cases) were matched one-to-one to 36 controls with later age of onset schizophrenia; the cases and controls were pair-matched on sex, race and socioeconomic status. Alternatively, in a matched prospective study, individuals are matched on exposure status. For example, individuals could be matched by sex, race and socioeconomic status, and then assigned to two different treatments and followed over time to determine whether the patients respond to the treatments. In these study designs, there are J 2 × 2 tables with one matched pair each. That is, the total sample size for each 2 × 2 table is 2. Even though each 2 × 2 table has only two subjects, assuming the number of matched pairs J is large, the Cochran–Mantel–Haenszel test can be used. In this case, the Cochran–Mantel–Haenszel test reduces to a test specific to matched paris, McNemar’s test: χ2 =

[n10 − n01 ]2 , n10 + n01

which has an approximate chi-square distribution with 1 degree of freedom for large J, where n10 is the number of matched pairs in which the case is exposed and the control is unexposed (or the exposed subject is a success and the unexposed subject is a failure) and n01 is the number of matched pairs in which the case is unexposed and the control 17

CHAPTER 2 Table 2.9 Complications during pregnancy and birth for 36 matched pair cases and controls. Controls

Cases

Absent Present

Absent

Present

23 9

4 0

is exposed (or the exposed subject is a failure and the unexposed subject is a success). An exact test based on the binomial distribution can be used when J (and particularly n10 + n01 ) is small. Matching one case (or exposed individual) to one control (or unexposed individual) is desirable because it maximises the power of the study for a given total sample size. However, when the number of cases is limited but a greater number of controls are available (e.g. in a rare disease setting), study designs matching one case to multiple controls are common. Because the total number of subjects nj++ can vary across partial tables, the Cochran–Mantel–Haenszel test can accommodate an arbitrary number of controls for each case. In addition, conditional logistic regression, which will be discussed in Section 2.6, also accommodates matched designs other than matched pairs and offers many of the advantages of logistic regression to matched studies.

2.4.3 Example McNemar’s test can be used to test for an association between birth complications and age of onset of schizophrenia using the data from Table 2.9. For this example, n10 is the number of pairs for which the case with earlier onset schizophrenia experienced birth complications but the control did not and equals 9, and n01 is the number of pairs for which the control experienced birth complications but the case with earlier onset schizophrenia did not and equals 4. If the large-sample test were applied, the test statistic would be χ2 = 1.92, and the p-value would be 0.17. Because n10 + n01 is small, exact methods are appropriate in this case, and would result in a p-value of 0.27. Therefore, we would conclude there is no evidence of an association between birth complications and age of onset of schizophrenia from this study. 18

2.5 Logistic regression In this section we consider how the relationships in multi-way contingency tables, and more complicated designs, can be explored using regression methods known as logistic regression. Logistic regression is one of the most widely used methods for the analysis of binary data. It is used to examine and describe the relationship between a binary response variable Yi (e.g. 1 = ‘success’ or 0 = ‘failure’) and one or more covariates for i = 1, . . . , n independent subjects. The covariates can be continuous or categorical (e.g. indicator variables). Denoting the two possible outcomes for Yi by 0 and 1, the probability distribution of the response variable is the Bernoulli distribution with probability of success pi . In common with linear regression, the primary objective of logistic regression is to model the mean of the response variable, given a set of covariates. Recall that with a binary response, the mean of Yi is simply the probability that Yi takes on the value 1, pi . However, what distinguishes logistic regression from linear regression is that the response variable is binary rather than continuous in nature. This has a number of consequences for modelling the mean of the response variable. For ease of exposition, we will first consider the simple case where there is only a single predictor variable, say xi . Generalisations to more than one predictor variable will be considered later. Since linear models play such an important and dominant role in applied statistics, it may at first seem natural to assume a linear model relating the mean of Yi to xi , pr[Yi = 1|xi ] = pi = β0 + β1 xi

(2.8)

However, expressing pi as a linear function is problematic since it violates the restriction that probabilities must lie within the range from 0 to 1. As a result, for sufficiently large or small values of xi , the linear model given by Equation 2.8 will yield probabilities outside of the permissible range. A further difficulty with the linear model for the probabilities is that we often expect a nonlinear relationship between pi and xi . For example, a 0.2 unit increase in pi might be considered more ‘extreme’ when pi = 0.1 than when pi = 0.5. In terms of ratios, the change from pi = 0.1 to pi = 0.3 represents a threefold or

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

g(pi ) = β0 + β1 xi .

(2.9)

However, the most commonly used in practice are 1 Logit or logistic function: g(pi ) = log[pi /(1 − pi )] 2 Probit or inverse normal function: g(pi ) = −1 (pi ), where  is the standardised normal cumulative distribution function 3 Complementary log–log function: g(pi ) = log [− log(1 − pi )]. We note that all of these transformations are very closely related when 0.2 < pi < 0.8, and in a sense only differ in the degree of ‘tail-stretching’ outside of this range. Indeed, for most practical purposes it is not possible to discriminate between a data analysis that is based on, for example, the logit and probit functions. To discriminate empirically between probit and logistic regression would, in general, require very large numbers of observations. However, the logit function does have a number of distinct advantages over the probit and complementary log–log functions which probably account for its more widespread use in practice. Later in this chapter we will consider some of the advantages of the logit or logistic function. When the logit or logistic function is adopted, the resulting model logit(pi ) = log[pi /(1 − pi )] = β0 + β1 xi ,

p

then 1−pi is the odds of success. Consequently, logisi tic regression assumes a linear relationship between the log odds of success and xi . Note that this simple model can be expressed equivalently in terms of pi , pi =

exp(β0 + β1 xi ) . 1 + exp(β0 + β1 xi )

(2.11)

We must emphasise that Equations 2.10 and 2.11 are completely equivalent ways of expressing the logistic regression model. Expression 2.10 describes p how the log odds, log( 1−pi ), has a linear relationship i with xi , while expression 2.11 describes how pi has an S-shaped relationship with increasing values of β1 xi ; although, in general, this relationship is approximately linear within the range 0.2 < pi < 0.8 (see Figure 2.1 for a plot of pi versus xi when β0 = 0.5 and β1 = 0.9). Observe that the expression on the right of (Equation 2.11) cannot yield a value that is either negative or greater than 1. That is, the logistic transformation ensures that the predicted probabilities are restricted to the range from 0 to 1.

1.0

0.8 Probability of Success

200% increase, whereas the change from pi = 0.5 to pi = 0.7 represents only a 40% increase. In a sense, the units of measurement for a probability or proportion are often not considered to be constant over the range from 0 to 1. The linear probability model given by Equation 2.8 simply does not take this into consideration when relating pi to xi . To circumvent these problems, a nonlinear transformation is usually applied to pi and the transformed probabilities are related linearly to xi . In particular, a transformation of pi , say g(pi ), is chosen so that it maps the range of pi from (0, 1) to (−∞, ∞). Since there are many possible transformations, g(pi ), that achieve this goal, this leads to an extensive choice of models that are all of the form

0.6

0.4

0.2

0.0 −4

(2.10)

−2

0

2

4

x

is known as the logistic regression model. Recall from Section 2.3.1 that if pi is the probability of success,

Fig 2.1

Plot of logistic response function.

19

CHAPTER 2

and xi = 1. Let pi (xi = j), denote the probability of success when xi = j, for j = 0, 1. Then,

Finally, note that 1 − pi = so that the odds,

1 , 1 + exp(β0 + β1 xi ) pi 1−pi ,

β1 = (β0 + β1 ) − β0 = logit[pi (xi = 1)] − logit[pi (xi = 0)]   pi (xi = 1) × [1 − pi (xi = 0)] = log pi (xi = 0) × [1 − pi (xi = 1)]

is simply exp(β0 + β1 xi ).

2.5.1 Interpretation of logistic regression coefficients Next we consider the interpretation of the logistic regression coefficients, β0 and β1 , in Equation 2.10. In simple linear regression, recall that the interpretation of the slope of the regression is in terms of changes in the mean of Yi for a single unit change in xi . Similarly, the logistic regression slope, β1 , in Equation 2.10 has interpretation as the change in the log odds of success for a single unit change in xi . Equivalently, a single unit change in xi increases or decreases the odds of success multiplicatively by a factor of exp(β1 ). Also, recall that the intercept in simple linear regression has interpretation as the mean value of the response variable when xi is equal to 0. Similarly, the logistic regression intercept β0 , has interpretation as the log odds of success when xi = 0. Note that, for case–control studies, the intercept β0 cannot be validly estimated since it is determined by the proportions of ‘successes’ (Y = 1) and ‘failures’ (Y = 0) selected by the study design. However, in many studies, there is far less scientific interest in the intercept than in the slope. For the special case where xi is dichotomous, taking values of 0 and 1, the logistic regression slope, β1 , has a simple and very attractive interpretation. Consider the two possible values for pi when xi = 0

which is the log of the OR (or cross-product ratio) in the 2 × 2 table of the cross-classification of Yi and xi (see Table 2.10). Thus, exp(β1 ) has interpretation as the OR of the response for the two possible values of the covariate. The OR has many appealing properties that probably account for the widespread use of logistic regression in many areas of application. First, as was noted earlier, the OR does not change when rows and columns of the 2 × 2 table are interchanged. This implies that it is not necessary to distinguish which variable is the response and predictor variable in order to estimate the OR. Furthermore, as noted in the previous sections, a very appealing feature of the OR, exp(β1 ), is that it is equally valid regardless of whether the study design is prospective, crosssectional or retrospective. That is, logistic regression provides an estimate of the same association between Yi and xi in all three study designs. Finally, in psychiatric studies where Yi typically denotes the presence or absence of a disease or disorder, the OR is often interpreted as an approximation to the RR p(x =1) of disease, p(xi =0) . When the disease is rare, and pi i is reasonably close to 0 in both of the risk groups (often known as the ‘rare disease’ assumption), the OR provides a close approximation to the RR. Retrospective designs are especially common in psychiatry

Table 2.10 Cross-classification probabilities for logistic regression of Y on x.

Y 1

1

p(x = 1) =

0

exp(β0 + β1) 1 + exp(β0 + β1)

1 − p(x = 1) =

1 1 + exp(β0 + β1)

Total

1.0

x 0

20

p(x = 0) =

exp(β0) 1 + exp(β0)

1 − p(x = 0) =

1 1 + exp(β0)

1.0

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

where the possible outcomes of interest are very rare. Although the RR cannot be estimated from a retrospective study, the OR can be used to provide an approximation to the RR. Extra care is necessary when interpreting the OR as an approximation to the RR in prospective studies. In many prospective studies the binary event is relatively common (say greater than 10%) and the ‘rare disease’ assumption no longer holds; in these settings, the OR can be a very poor and unreliable approximation to the RR and should not be given such an interpretation.

2.5.2 Hypothesis testing and confidence intervals for logistic regression parameters Often, we are interested in testing for an association between the predictor in our logistic regression model and the outcome, or, equivalently, testing H0 : β1 = 0. As for 2 × 2 table methods, Wald, likelihood ratio and score statistics can be used for this test. A Wald test statistic can be obtained using the result that the estimate of β1 divided by its standard error (s.e.) approximately follows a N(0, 1) distribution in large samples. A LRT statistic can be obtained by comparing the log likelihood for the full model with the predictor included to the log likelihood for a reduced model including only the intercept β0 ; the former is at least as large as the latter. In large samples, twice the difference between the maximised log likelihoods for the full and reduced models approximately follows a chi-square distribution with 1 degree of freedom. Two-sided Wald confidence limits for β1 can be obtained using the result that βˆ 1 follows an approximate normal distribution; the confidence limits are given by the formula βˆ 1 ± zα/2 ∗ s .e.(βˆ 1 ). Just as we ˆ can exponentiate β1 to get an estimate of the OR comparing the odds of disease for a unit change in x1 , we can exponentiate the lower and upper limits of the confidence interval for β1 to get a confidence interval for the OR. Estimates of β1 (or, alternatively, its associated OR), its standard error and the log likelihood for the model are available from the output from logistic regression routines from popular statistical software. Test statistics and p-values for tests that β1 = 0 and Wald 95% confidence intervals are often also included automatically. Likelihood ratio and score test statistics can sometimes be requested.

Although Wald tests and confidence intervals are standard output from software for fitting logistic regression, we caution the reader that in certain circumstances the performance of Wald tests (and confidence intervals) can be somewhat irregular and lead to misleading conclusions. As a result, we recommend that LRTs (and confidence intervals) be used whenever possible.

2.5.3 Example: Logistic regression with a single binary covariate We now return to the Table 2.1 data from the first-episode major affective disorders with psychosis study and show that we can obtain identical results using large-sample methods for 2 × 2 contingency tables (as reported in Section 2.3.2) and logistic regression. Recall that our interest is in the association between Axis I comorbidity and 2-year functional recovery in this group of patients. Using logistic regression, we fit the model: logit[pr(Recoveryi = 1)] = β0 + β1 ∗ Comorbidityi , (2.12) where Recoveryi is an indicator variable coded 1 if the ith subject recovered and 0 otherwise, and Comorbidityi is an indicator variable coded 1 if the ith subject had Axis I Comorbidity and 0 otherwise. The following are the results: βˆ

ˆ s.e.(β)

Z

p > |Z| 95% CI

−0.2624 0.1881 −1.39 0.163 −0.6310, 0.1063 Comorbidity −0.7185 0.3343 −2.15 0.032 −1.3737, −0.0632 Intercept

The estimate of the OR comparing the odds of recovery in patients with and without Axis I comorbidities is exp(−0.7185) = 0.49, and the 95% confidence interval for the OR is exp(−1.3737, −0.0632) = (0.25, 0.94). The Wald test statistic for no association (or, equivalently, for H0 : β1 = 0 or H0 : OR = 1), which appears in the table, is Z = −2.15, with an accompanying p-value of 0.03. We can obtain the LRT statistic for no association by fitting the model with the intercept as 21

CHAPTER 2

the only covariate, which has a log-likelihood of −119.8066, and comparing it to the log likelihood from the model with both the intercept and comorbidity as covariates, −117.4037. The LRT statistic is χ21 = 2 ∗ [−117.4037 − (−119.8066)] = 4.81. The associated p-value, which can be obtained using statistical software or estimated from chi-square distribution tables, is 0.03. These results and their interpretation are identical to those obtained using methods for 2 × 2 contingency tables and reported in Section 2.3.2.

2.5.4 Multiple logistic regression So far, we have only considered the simple case where there is a single covariate xi . Next, we consider the extensions of Equations 2.10 and 2.11 to the case where there are two or more covariates. Recall that, in Section 2.4, we applied methods for stratified contingency tables to the first-episode major affective disorders with psychosis study data to test that the OR comparing patients with and without comorbidities adjusted for sex equals 1. Methods for stratified contingency tables are useful when adjusting for a small number of categorical covariates. However, multiple logistic regression has important advantages over stratified contingency table methods when the number of categorical covariates is larger or when we want to adjust for quantitative covariates. For example, using the first-episode data, we may want to test that the OR adjusted for both sex and age equals 1 and to obtain an estimate of the adjusted OR without classifying age into arbitrary categories. When there are many covariates, the logistic regression model becomes, log[pi /(1 − pi )] = β0 + β1 xi1 + β2 xi2 + · · · + βK xiK ,

2.5.5 Example: Multiple logistic regression To obtain an estimate of the OR for comorbidity adjusted for sex and age and to test that the adjusted OR equals one, we fit the following multiple logistic regression model to the first-episode major affective disorders with psychosis data: logit[pr(Recoveryi = 1)] = β0 + β1 ∗ Comorbidityi + β2 ∗ Malei + β3 ∗ Agei , (2.14) where Malei is an indicator variable coded 1 if the ith subject is male and 0 if the ith subject is female and Agei is the age of the ith subject in decades. The following results are obtained:

(2.13)

where xi1 , xi2 , . . . , xiK are the K covariates. The logistic regression coefficients in Equation 2.13 have the following interpretations. The logistic regression intercept, β0 , now has interpretation as the log odds of success when all covariates equal 0, that is when xi1 = xi2 = · · · = xiK = 0. Each of the logistic regression slopes, βk (for k = 1, . . . , K), has interpretation as the change in the log odds of success for a 22

single unit change in xik given that all of the other covariates remain constant. Note that the appealing property of logistic regression that the same OR can be estimated from either a prospective or retrospective study design readily generalises when xik is quantitative rather than dichotomous, and also when there are two or more predictor variables. Methods for hypothesis testing and constructing confidence intervals also generalise easily from the predictor in a simple logistic regression model (β1 ) to a predictor in a multiple logistic regression model βk . Expressions for Wald test statistics and confidence intervals for (βk ) can be obtained by substituting βk for β1 in the relevant portions of Section 2.5.2. LRTs of βk = 0 can be constructed by comparing the fit of the full model with βk included to the fit of a reduced model with all covariates except βk included. Twice the difference between the maximised log likelihood for the full model and the maximised log likelihood for the reduced model still approximately follows a chi-square distribution with one degree of freedom.

βˆ

ˆ s.e.(β)

Z

p > |Z| 95% CI

−1.4019 0.4955 −2.83 0.005 −2.3730, −0.4307 Comorbidity −0.4845 0.3496 −1.39 0.166 −1.1697, 0.2008 Male 0.0049 0.3243 0.01 0.988 −0.6307, 0.6404 Age 0.3107 0.1094 2.84 0.004 0.0963, 0.5250 Intercept

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

The estimate of the OR for comorbidity adjusted for sex and age is exp(−0.4845) = 0.62, and its 95% confidence interval is exp(−1.1697, 0.2008) = (0.31, 1.22). Holding sex and age constant, we estimate that the odds of two-year functional recovery is 38% lower for patients with Axis I comorbidity when compared to patients without Axis I comorbidity. However, note from the 95% confidence interval that our data are consistent with odds of recovery up to 22% higher for patients with Axis I comorbidity. In addition, the Wald test statistic for testing that the adjusted OR equals one is Z = −1.39 with an associated p-value of 0.17, and the LRT statistic is χ21 = 1.95 with an associated p-value of 0.16. Using either test we conclude there is no association between Axis I comorbidity and 2-year functional recovery after adjusting for sex and age. We can also use the results from the multiple logistic regression to obtain estimates and test statistics for the other covariates in the model. The estimated OR comparing odds of recovery in males versus females is 1.00 (95% confidence interval: 0.53, 1.90), and we conclude from the Wald test that there is no evidence of an association between sex and recovery after adjusting for Axis I comorbidity and age (Z = 0.01, p = 0.99). On the other hand, the estimated OR comparing odds of recovery for a 10-year age increase is 1.36 (95% confidence interval: 1.10, 1.69). Adjusting for Axis I comorbidity and sex, the odds of two-year functional recovery increases with age (Z = 2.84, p = 0.004); for every decade age increase, we estimate that the odds of recovery is 36% higher.

2.5.6 Categorical predictors with more than two levels in logistic regression Section 2.3.3 presented contingency table methods that could be used to test for independence with predictors or outcomes with more than two categories. This section describes how logistic regression accommodates predictors with more than two categories, either with or without adjustment for additional covariates. (A later section describes extensions of logistic regression that accommodate outcomes with more than two categories.) For K unordered categories, a test for independence can be obtained by adding K − 1 indicator or ‘dummy’ variables as

covariates in the regression, where the kth indicator variable is coded 1 for subjects in the kth category and 0 for all other subjects (so that subjects in the remaining ‘reference’ category are coded 0 for all K − 1 indicator variables). A LRT for no association can be conducted by comparing the log likelihood for the model containing the predictor to the log likelihood for the model with the K − 1 indicator variables corresponding to the predictor removed; the LRT statistic follows a chi-square distribution with K − 1 degrees of freedom. Wald and score hypothesis tests are also available. However, when a predictor has three or more categories, the Wald test of no association is sometimes not available from standard logistic regression output and must be requested. For ordered categories, a test for independence can be conducted by assigning scores to each level of the predictor and then using the score as a covariate in the regression model. For example, the scores 1, 2 and 3 could be assigned to the categories mild, moderate and severe. The Z statistic for the covariate then corresponds to a test for no association, and interpretation of the corresponding regression parameter is similar to the interpretation of a regression parameter for a quantitative predictor. For example, the OR for the severity predictor would compare the odds of the outcome for a one category increase in severity, either moderate versus mild or severe versus moderate. This approach is most appropriate when the association between the score and outcome is approximately linear.

2.5.7 Example: Logistic regression with a three-level predictor In Section 2.3.4, we performed tests for independence between type of onset of first-episode affective disorder with psychosis (categorised as chronic, subacute or acute) and 2-year functional recovery. Equivalent tests can be performed using logistic regression by fitting the model: logit[pr(Recoveryi = 1)] = β0 + β1 ∗ Subacutei + β2 ∗ Acutei ,

(2.15)

where Subacutei is an indicator variable coded 1 if the ith subject had subacute onset and 0 otherwise, Acutei is an indicator variable coded 1 if the ith 23

CHAPTER 2

subject had acute onset and 0 otherwise, and chronic onset is the reference category. The following results are obtained:

we would use the model: logit[pr(Recoveryi = 1)] = β0 + β1 ∗ Comorbidityi + β2 ∗ Malei + β3 ∗ Comorbidityi ∗ Malei

βˆ

ˆ s.e.(β)

p > |Z|

95% CI

Intercept −0.6061 0.2930 −2.07

0.039

Subacute

0.1071 0.4247

0.25

0.801

Acute

0.2007 0.3761

0.53

0.594

−1.1804, −0.0318 −0.7253, 0.9396 −0.5364, 0.9377

Z

Exponentiating the parameters for subacute and acute onset provides estimates of the ORs comparing odds of recovery for subacute and acute onset respectively versus chronic onset, and the Z statistics for these two parameters are for separate tests that these ORs are equal to 1. However, our primary interest is in the overall test for independence between onset and recovery. The log likelihood for this model is −113.421, and the log likelihood for the model with an intercept only is −113.565. The resulting LRT statistic for independence is χ22 = 0.29 (i.e. twice the difference in log likelihoods), with an associated p-value of 0.87. These results are identical to the LRT results from Section 2.3.4, and our conclusions are the same; that is, there is no association between type of onset and 2-year functional recovery. In this case, the Wald test statistic is also χ22 = 0.29 with a p-value of 0.87.

2.5.8 Interactions in logistic regression In Section 2.4, we introduced a test for interaction using methods for contingency tables. Recall that an interaction between two predictor variables is present when the OR for one predictor differs according to the value of the other predictor. For example, for the data from Table 2.7, we would state that there is an interaction between comorbidity and sex if the OR comparing odds of recovery with and without comorbidity differs between males and females. We can allow for interaction in logistic regression models by multiplying the covariates for the predictors involved in the interaction and adding them as additional covariates to the regression model. For example, to test for an interaction between comorbidity and sex, 24

(2.16) For this model, exp(β1 ) is the OR comparing odds of recovery in female patients with and without comorbidity, and exp(β1 + β3 ) is the OR comparing odds of recovery in male patients with and without comorbidity. These two ORs are equal if and only if β3 = 0; therefore, the test of H0 : β3 = 0 is a test of no interaction between comorbidity and sex. Using logistic regression, tests for interaction are also straightforward for quantitative predictors, categorical predictors with more than two levels, and interactions among more than two predictors.

2.5.9 Example: Logistic regression with interaction Fitting the model from Equation 2.16 to the data from Table 2.7 results in the following output: βˆ

ˆ s.e.(β)

Z

p > |Z| 95% CI

−0.2657 0.2771 −0.96 0.338 −0.8089, 0.2775 Comorbidity −0.4881 0.5105 −0.96 0.339 −1.4887, 0.5125 Male 0.0062 0.3774 0.02 0.987 −0.7335, 0.7459 Comorbidity −0.3838 0.6771 −0.57 0.571 −1.7110, * Male 0.9433 Intercept

The estimated OR comparing odds of 2-year functional recovery for patients with and without Axis I comorbidity is exp(−0.4881) = 0.61 for females and exp(−0.4881 − 0.3838) = 0.42 for males. Note that we can calculate a confidence interval for the OR for females but not for males from the information in the output; because the OR for males is calculated by summing two parameter estimates, the covariance between the two parameter estimates would be required in order to calculate the confidence interval. The Wald test statistic for no interaction is Z = −0.57, with an associated p-value of 0.57. The LRT statistic (obtained by comparing the loglikelihood for this model to the log-likelihood for

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

the model with covariates for comorbidity and sex but not their interaction) is 0.32 with an associated p-value of 0.57. We conclude that there is no interaction between Axis I comorbidity and sex; that is, the OR comparing the odds of functional recovery for patients with and without Axis I comorbidity is the same for males and females. These results agree with the Breslow–Day test results from Section 2.4.1.

2.5.10 Goodness-of-fit When a multiple logistic regression model has been used to draw conclusions from a study, we should check the fit of the model to the study data. One way to check the fit of a model is to use statistical tests for goodness-of-fit; in the absence of significant evidence of poor fit from these test statistics, we conclude the fit of our model is adequate. The deviance (based on the likelihood ratio statistic) or the Pearson chi-square can be used as a goodness-of-fit statistic if, at each observed covariate pattern, the data can be grouped. That is, if there are ni subjects with the same covariate values (and hence the same Bernoulli distribution), they can be treated as a binomial sample and a test of goodness-of-fit can be based on the comparison of the observed and expected (or predicted) counts in each covariate pattern. Alternatively, if the covariates are quantitative rather than categorical, Hosmer and Lemeshow [10] proposed a goodness-of-fit statistic similar to the Pearson chi-square, which can be calculated after grouping individuals on the basis of having similar values of the predicted probability pi . Evidence of poor fit can reflect a variety of problems with our model, such as an inappropriate choice of transformation function, failure to include important interaction terms, or inappropriate assumption of linearity for quantitative or ordered categorical covariates, and is an indication that we should revisit the assumptions made during the modelling process.

2.6 Advanced topics In this section we briefly review a number of more advanced topics that can be considered extensions of the standard logistic regression model. Many of these methods have been somewhat slow to move into

the mainstream of psychiatric research. However, with their recent implementation in widely available statistical software, these methods are starting to be more widely applied.

2.6.1 Conditional logistic regression The previous section showed that logistic regression can be used to perform analyses similar to those using contingency table methods but with more complex extensions and applications. This section introduces a related technique known as conditional logistic regression, which extends many of the benefits of logistic regression to studies with matched designs. In matched study designs individuals are stratified on the basis of variables thought to be related to the outcome variable of interest. For example, age and years of education are two variables commonly used to define strata in many psychiatric studies. The conditional logistic regression model used to analyse matched data is log[pij /(1 − pij )] = αi0 + β1 xij1 + β2 xij2 + · · · + βK xijK .

(2.17)

Note that this is similar to the standard logistic regression model, except that the probability of success and the predictors are now indexed by i and j instead of i alone to indicate that they apply to the jth individual from the ith strata (e.g. matched pair). Note also that the common intercept β0 in standard logistic regression has been replaced in Equation 2.17 by a stratum-specific intercept αi0 . Parameter estimates from conditional logistic regression can be interpreted in a similar way as parameter estimates from standard (or unconditional) logistic regression, and conditional logistic regression offers the same capabilities as standard logistic regression with a few exceptions. One is that the stratum-specific intercepts cannot be estimated (and will not be included in conditional logistic regression output). This is because the method of estimation (discussed later) effectively eliminates them to ensure that the β’s are estimated without any bias. This is usually not a concern since, as for standard logistic regression, these intercepts are generally not of scientific interest. Second, because the model includes stratum-specific intercepts, the β’s now have 25

CHAPTER 2

stratum-specific interpretations in terms of changes in the log odds of success for within-stratum changes in the covariates. For example, β1 has interpretation in terms of changes in the log odds of success for a single unit change in xij1 within the ith stratum (i.e. comparing two individuals within the same stratum that happen to differ by one unit in the covariate). Third, the associations between any variables used for matching (or any other covariates that are constant within strata) and the outcome cannot be quantified. This is because the method of estimation is based entirely on variation within a stratum; conditional logistic regression cannot be used to estimate the effect of a covariate that varies only between strata (but not within a stratum). Returning to the example from Section 2.4.2, a study examining the association between birth complications and age of onset of psychosis that matches on sex, conditional logistic regression cannot quantify the association between sex and age of onset of psychosis because, by study design, sex does not vary within each stratum. However, it is still possible to test for interactions between variables used for matching and other predictors. Next we consider estimation of the model parameters. One approach to fitting this model would be to attempt to estimate all of the parameters, including the stratum-specific intercepts. However, for matched designs, the number of strata grows as the sample size increases, which means that the number of parameters would be large relative to the sample size no matter how big a sample was collected. For example, in a matched-pair design with n pairs (i.e. two subjects in each stratum), such an analysis would require the estimation of n + K parameters from a sample of only 2n observations. It should not be surprising that this proliferation of stratum-specific intercepts causes problems for estimation; it also causes problems with the properties of standard maximum likelihood estimates of the model parameters. To avoid these problems, conditional logistic regression maximises a likelihood for the conditional distribution (and hence the term ‘conditional’ logistic regression) that eliminates these stratum-specific intercepts and bases estimation of the associations between the predictors and outcome entirely on information from within the strata. 26

2.6.2 Exact logistic regression Like many methods for contingency tables, logistic regression as traditionally implemented (i.e. maximum likelihood logistic regression) relies on large sample theory for the validity of its results. Maximum likelihood logistic regression can perform poorly when the sample size is small, the probability of success is near one or zero, or we have an insufficient number of successes or failures for certain combinations of our covariates. Error messages from statistical software, very large or small parameter estimates, or very wide confidence intervals can sometimes alert us to these problems, though logistic regression can still have poor performance due to sparse data even when the problem is not evident from the distribution of individual covariates or from an examination of the results [11]. Exact logistic regression [12] is a method for fitting logistic regression models that produces valid estimates, test statistics and confidence intervals even for small datasets or sparse data. For example, exact logistic regression was used to study psychiatric and social predictors of attempted suicides in a sample of Indian women [13]. In this study, the total number of participants was fairly large (2494), but the number of suicide attempts was relatively small (19). As a result, very small numbers of successes (suicide attempts) were observed for some predictors, and exact logistic regression was an appropriate analysis strategy. The relationship of exact logistic regression to maximum likelihood logistic regression is similar in some ways to the relationship of Fisher’s exact test to large-sample methods for R × C contingency tables. However, whereas Fisher’s exact test conditions on the row and column totals in order to derive the distribution of the test statistic, exact logistic regression conditions on the so-called sufficient statistics for the remaining parameters in the model when estimating each parameter. The sufficient statistics for the parameters are determined by the number of successes for different values of the corresponding covariates. Like other exact methods, exact logistic regression guarantees that tests conducted at significance level α have a type I error rate less than or equal to α, and that 95% confidence intervals have at least 95% coverage even for small sample sizes and sparse data.

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

It can be implemented by several popular statistical software packages, and parameter estimates and confidence intervals have an interpretation identical to those for maximum likelihood logistic regression. Some disadvantages are that it may be overly conservative in settings when maximum likelihood logistic regression performs adequately and that it can be computationally intensive, especially when quantitative covariates or a large number of categorical covariates are included in the model. In principle, exact logistic regression can be applied in settings with multiple covariates; however, greater care is required when attempting to fit complex models. When feasible, exact logistic regression is an attractive alternative to maximum likelihood logistic regression in small sample and sparse data settings.

2.6.3 Multinomial regression models A major focus of this chapter has been on logistic regression modelling of a binary outcome. For some applications, however, the outcome variable of interest is categorical with more than two levels. For example, in a study of trauma in a high-risk AfricanAmerican sample [14], response to trauma was categorised as currently ill (current psychiatric disorder), recovered (past history of one or more psychiatric disorders) or resilient (no history of psychiatric disorder). Predictors of response to severe trauma in this population were examined using polytomous logistic regression. In this section we introduce multinomial models for categorical outcomes with more than two levels by first considering the case of such a nominal categorical variable. Suppose the outcome for individual i is categorical with J levels and let Yi equal 1 with probability pi1 , equal 2 with probability pi2 , and so on. In general, Yi equals j with probability pij , j = 1, . . . , J. We can introduce some additional notation that will make the extension of logistic regression to this setting more transparent. Suppose we let Yij equal 1 if Yi = j, and equal 0 otherwise, for j = 1, . . . , J. Then, pij = pr[Yi = j|xi1 , . . . , xiK ] = pr[Yij = 1|xi1 , . . . , xiK ]. When J > 2, the extension of the logistic regression model known as polytomous (or multinomial) logistic regression is appropriate. In polytomous logistic regression, we form J − 1

non-redundant logits:   pr[Yi = j|xi1 , . . . , xiK ] log pr[Yi = J|xi1 , . . . , xiK ]   pr[Yij = 1|xi1 , . . . , xiK ] = log pr[YiJ = 1|xi1 , . . . , xiK ]   pij = log = βj0 + βj1 xi1 + · · · + βjK xiK piJ j = 1, . . . , J − 1, where the regression parameters, βj0 , βj1 , . . . , βjK , can be different for each level j. In this notation, the last category J is referred to as the ‘reference’ category. It can also be shown that, for j = 1, . . . , J − 1, pij =

exp[βj0 + βj1 xi1 + · · · + βjK xiK ] J−1 1 + j=1 exp[βj0 + βj1 xi1 + · · · + βjK xiK ]

Note that this polytomous logistic regression model is more appropriate when the categorical variable is nominal. In other settings, the categorical outcome is ordinal. For example, in a study of predictors of remission in patients over age 60 treated for depression, the outcome was categorised as no remission, partial remission or full remission [15]. For ordinal outcomes a variety of regression models can be used, including mean score models and models of a logistic regression form. The logistic models for ordinal data include the continuation odds model, the adjacent category logit and the cumulative logit models [16]. Here, we briefly discuss the cumulative logistic proportional odds model, one of the most widely used regression models for ordinal data. To formulate an ordinal response model, we form logits of the cumulative probabilities. Recall, pij = pr[Yij = 1|xi1 , . . . , xiK ]. We define the cumulative probabilities as Fij = pr[Yi ≤ j|xi1 , . . . , xiK ] = pi1 + . . . + pij . In the previous example, Fi2 is the probability of a response of (i) no remission or (ii) partial remission. The logit of Fij ,     pi1 + · · · + pij Fij = log logit(Fij ) = log 1 − Fij pi,j+1 + . . . + piJ is often referred to as the ‘cumulative’ logit, and these cumulative logits can be related to covariates in the following proportional odds model, logit(Fij ) = αj + β1 xi1 + · · · + βK xiK . 27

CHAPTER 2

Note that the original multinomial probabilities can be expressed in terms of the cumulative probabilities via pij = Fij − Fi,j−1 . Inferences about the ‘cumulative logits’ or ‘cumulative’ log ORs can be made similarly to inferences for standard logistic regression. For example, with remission category as the outcome, if xi1 is an indicator for comorbid dysthymia (an important predictor in the Hybels et al. [15] study), exp(β1 ) is the OR comparing the odds of full or partial remission versus no remission. A property of the proportional odds model is that exp(β1 ) is also the OR comparing the odds of full remission versus partial or no remission for patients with and without comorbid dysthymia.

2.6.4 Clustered categorical data In the previous sections we have considered regression models for a single categorical outcome. However, multivariate categorical response data commonly arise in a number of applications in psychiatry. That is, two or more measurements of the response are often obtained in a block or cluster and the categorical responses within a cluster are expected to be positively correlated. When this occurs, the responses from any pair of members of the same cluster are expected to be more closely related than the responses from a pair belonging to different clusters. Some common examples where data arise in clusters include repeated measures or longitudinal studies and studies on families, communities or other naturally occurring groups. For example, in a study of the familial association between rheumatic fever and obsessive–compulsive spectrum disorders, each cluster consisted of first-degree relatives of either a case with rheumatic fever or a control [17]. The important aspect of all of these studies is that the categorical responses within a cluster (e.g. the presence of obsessive–compulsive spectrum disorders in firstdegree relatives) cannot be regarded as independent of one another. There may be many reasons for the correlation among cluster members. For example, when the cluster is comprised of all the siblings within a family the correlation among siblings may be due to shared (or at least similar) genetic, environmental and social conditions. In a longitudinal study, where 28

the responses within a cluster represent measurements taken at different occasions, the categorical responses are expected to be positively correlated simply because they have been obtained on the same individual (or cluster). Whatever the underlying reasons for the correlation, failure to account for it in the analysis can lead to invalid inferences. That is, the standard application of logistic regression (or any methods that assume independent observations) in this setting is no longer appropriate. For the remainder of this section we focus on the case of clustered binary data; however, the methods we discuss apply more broadly to clustered categorical data. There are two general approaches for handling the analysis of clustered binary data. The first is to consider models for the joint distribution of the cluster of binary responses that explicitly account for the within-cluster correlation. There is an extensive statistical literature on this topic and the interested reader is referred to a review article by Pendergast et al. [18]. For the most part, these models can be computationally demanding and have only recently been implemented in commercially available statistical software. An alternative approach is to simply ignore the correlation among members of a cluster. That is, the analysis proceeds naively as though the binary responses within a cluster can be regarded as independent observations, but later a correction is applied to ensure that valid standard errors are obtained. Note that in this ‘naive’ approach that ignores the within-cluster correlation the estimated logistic regression coefficients are valid, but their nominal standard errors are not. However, valid standard errors can be readily obtained using the well known empirical variance estimator, first proposed by Huber [19]. Thus, the analysis proceeds in two stages. In the first stage, the correlation among binary responses within a cluster is simply ignored and standard logistic regression is used to obtain estimates of the logistic regression coefficients. In the second stage, valid standard errors for the estimated logistic regression coefficients are obtained using an alternative, but widely implemented, variance estimator that properly accounts for the correlation among the binary responses. The chief advantage of this approach is that it can be readily implemented using standard statistical software for logistic regression.

ANALYSIS OF CATEGORICAL DATA: THE ODDS RATIO AS A MEASURE OF ASSOCIATION AND BEYOND

2.7 Concluding remarks This chapter presents an overview of statistical methods for categorical (and primarily binary) outcomes, with an emphasis on the OR and its applications in psychiatry. The OR is a particularly useful measure of association because it can be estimated from a number of common study designs. Contingency table methods provide intuitive ways of examining the associations among a limited number of categorical variables from these study designs. Logistic regression offers many of the same advantages of contingency table methods but also provides an efficient method for incorporating an arbitrary number of categorical and quantitative covariates. Logistic regression also provides a framework for extensions to more complex study designs often encountered in psychiatry.

[6] [7] [8]

[9]

[10]

[11]

[12]

2.8 Further reading A very comprehensive description of statistical methods for analysing categorical data can be found in the classic textbook by Agresti [20], and a thorough overview of logistic regression methods with an emphasis on applications can be found in the text Applied Logistic Regression by Hosmer and Lemeshow [21].

References

[13]

[14]

[15]

[16] [17]

[1] Tohen, M., Hennen, J., Zarate, C.M. et al. (2000) Two-year syndromal and functional recovery in 219 cases of first-episode major affective disorder with psychotic features. Am. J. Psychiatry, 157, 220–228. [2] Brown, L.D., Cai, T.T. and DasGupta, A. (2001) Interval estimation for a binomial proportion. Statist. Sci., 16, 101–133. [3] Breslow, N.E. and Day, N.E. (1980) Statistical Methods in Cancer Research, The Analysis of Case–Control Studies, Vol. 1, World Health Organization, Lyon. [4] Wærn, M., Runeson, B.S., Allebeck, P. et al. (2002) Mental disorder in elderly suicides: a case–control study. Am J. Psychiatry, 159, 450–455. [5] Geda, Y.E., Roberts, R.O., Knopman, D.S. et al. (2008) Prevalence of neuropsychiatric symptoms in mild cognitive impairment and normal cognitive

[18]

[19]

[20] [21]

aging: population-based study. Arch. Gen. Psychiatry, 65, 1193–1198. Fisher, R.A. (1934) Statistical Methods for Research Workers, Oliver and Boyd, Edinburgh. Cochran, W.G. (1954) Some methods of strengthening the common χ2 tests. Biometrics, 10, 417–451. Mantel, N. and Haenszel, W. (1959) Statistical aspects of the analysis of data from retrospective studies of disease. J. Natl. Cancer Inst., 22, 719–748. Everitt, B.S. (1992) Some aspects of the analysis of categorical data, in A Handbook for Data Analysis in the Behavioral Sciences, Statistical Issues, Vol. 2 (eds G. Keren and C. Lewis), Lawrence Erlbaum Associates, Hillsdale, NJ, pp. 321–348. Hosmer, D.W. and Lemeshow, S. (1980) A goodnessof-fit test for the multiple logistic regression model. Commun. Stat., A10, 1043–1069. King, E.N. and Ryan, T.P. (2002) A preliminary investigation of maximum likelihood logistic regression versus exact logistic regression. Am. Stat., 56, 163–170. Mehta, C.R. and Patel, N.R. (1995) Exact logistic regression: theory and examples. Stat. Med., 14, 2143–2160. Maselko, J. and Patel, V. (2008) Why women attempt suicide: the role of mental illness and social disadvantage in a community cohort study in India. J. Epidemiol. Community Health, 62, 817–822. Alim, T.N., Feder, A., Graves, R.E. et al. (2008) Trauma, resilience, and recovery in a high-risk African-American population. Am. J. Psychiatry, 165, 1566–1575. Hybels, C.F., Blazer, D.G. and Steffens, D.C. (2005) Predictors of partial remission in older patients treated for major depression: the role of comorbid dysthymia. Am. J. Geriatr. Psychiatry, 13, 713–721. McCullagh, P. and Nelder, J. (1989) Generalized Linear Models, 2nd edn, Chapman & Hall, London. Hounie, A.G., Pauls, D.L., do Rosario-Campos, M.C. et al. (2007) Obsessive-compulsive spectrum disorders and rheumatic fever: a family study. Biol. Psychiatry, 61, 266–272. Pendergast, J.F., Gange, S.J., Newton, M.A. et al. (1996) A survey of methods for analyzing clustered binary response data. Int. Stat. Rev., 64, 89–118. Huber, P.J. (1967) The behavior of maximum likelihood estimates under nonstandard conditions, in Proceedings of the Fifth Berkeley Symposium on Mathematical Statistics and Probability. Vol. 1, Berkeley, CA: University of California Press, pp. 221–233. Agresti, A. (2002) Categorical Data Analysis, 2nd edn, John Wiley & Sons, Inc., New York. Hosmer, D.W. and Lemeshow, S. (2000) Applied Logistic Regression, 2nd edn, John Wiley & Sons, Inc., New York.

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3

Genetic epidemiology Stephen V. Faraone,1 Stephen J. Glatt1 and Ming T. Tsuang2,3 1 Departments

of Psychiatry and Behavioral Sciences and Neuroscience and Physiology, Medical Genetics Research Center, SUNY Upstate Medical University, NY, USA 2 Center for Behavioral Genomics, Department of Psychiatry, University of California, San Diego, CA, USA 3 Veterans Affairs San Diego Healthcare System, San Diego, CA, USA

3.1 Introduction Epidemiologists usually concern themselves with describing the distribution and determinants of disease as a function of exposure to some environmental variable. This leads naturally to the goal of finding environmental risk factors that cause illness. In contrast, geneticists focuses on genetic mechanisms and, in experimental studies, may even seek to strictly control the environment and eliminate environmental variance. Thus, epidemiologic research often treats genetic determinants as noise and environmental agents as the signal; genetic studies reverse the roles of genes and environment. Psychiatric genetics adopts the position of genetic epidemiology, which has been defined as, ‘a science that deals with aetiology, distribution and control of disease in groups of relatives and with inherited causes of disease in populations’ [1]. Genetic epidemiologists examine the distribution of illness within families with the goal of finding genetic and environmental causes of illness. Thus, psychiatric genetics considers both environmental and genetic risk factors – and their interaction – to be on an equal footing. This paradigm extends the epidemiologist’s concept of ‘exposure’ to genes and family relationships. Most psychiatric genetic research is predicated on an assumption that the pathway from genotype to phenotype

cannot be understood without reference to environmental agents that trigger illness in susceptible individuals. The debate ascribing the risk for psychiatric disorders to either nature or nurture has been laid to rest, as most of these conditions are now understood to arise from the combination of both. Current work seeks to define genetic and environmental risk factors, the magnitude of their contributions and how they interact. The methods of psychiatric genetic epidemiology have established the familial and heritable nature of various psychiatric disorders over the last several decades; they are now poised to unravel their underlying mechanisms in the years to come.

3.2 The chain of psychiatric genetic research Work in psychiatric genetics follows a series of progressive questions (Table 3.1). This chain of genetic epidemiologic research [2], is as follows: First, we ask ‘Is the disorder familial? Does it run in families?’ Second, ‘What is the relative magnitude of genetic and environmental contributions to disease aetiology and expression?’

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

31

CHAPTER 3 Table 3.1

Chain of psychiatric genetic research.

Questions

Methods

Is disorder familial? What are the relative contributions of genes and environment? What is mode of transmission? Where is the gene (or genes) located? What is the risk-conferring variants?

Family study Twin and adoption studies

Third, ‘How is disease transmitted from generation to generation?’ Fourth, ‘If genes mediate transmission, where are they located?’ Fifth, ‘What are the risk-conferring variants of the genes and what is the mechanism of disease?’ In modern practice, some questions are pursued before those ‘earlier’ in the chain have been addressed. This is due to the fact that ‘later’ questions are presumed to elucidate more specific risk factors than earlier ones, and because the technology for pursuing these later questions has advanced rapidly, making their wide-scale implementation highly feasible. It is a fallacy that the newest methods can obviate earlier ones, as there is no method devised to date that has been found capable of explaining all sources of variation in the liability towards a complex phenotype such as those in the realm of psychiatry. Thus, we start our introduction to the field of psychiatric genetic epidemiology with a review of its oldest methods and conclude by reviewing the latest molecular genetic techniques, with the understanding that each method is but one essential instrument in the genetic epidemiologist’s toolbox.

3.2.1 Is the disorder familial? This question can be addressed more easily than some others in genetic epidemiology, which is why it is often asked first; another reason for its primacy in the chain of research is that it provides the most fundamental direction for subsequent genetic epidemiologic studies. If a disorder shows familial transmission, follow-up with other methods is warranted, whereas if no familial resemblance for the trait is observed, investigations of the disorder would proceed in a different direction (e.g. environmental surveys). 32

Segregation analysis Linkage analysis Association analysis

Observations of disorders ‘running in families’ may come from clinicians who often treat patients from the same family. Once familiality is informally established in a clinical setting, it remains to be confirmed with a rigorous research design, known as the family study method.

3.2.1.1 Selection of probands A family study should use the blind case–control paradigm. The cases and controls used in genetic studies are known as probands. We select probands with the disorder from a source, that is ‘enriched’ with the diagnosis of interest. For example, patients in psychiatric clinics are more likely to have bipolar disorder than patients in a family practice clinic. Furthermore, patients in a bipolar speciality clinic are more likely to have bipolar disorder than patients in a general psychiatric clinic. Selection from clinics instead of the general population is useful because, to achieve an adequate number of cases from the general population we would need to screen many individuals. This is costly and of dubious benefit. Also, multiple stages of ascertainment increase the probabilities of ill probands being ‘true cases’ and of unaffected or ‘control’ probands not having the disorder under study. The positive predictive power of a diagnosis (the proportion of those with the disorder among all patients receiving the diagnosis) increases as the base rate of the disorder being diagnosed increases [3]. Thus, multiple-stage ascertainment increases positive predictive power by using clinic status to increase the proportion of ‘true cases’ in the sample. This method of increasing positive predictive power will increase the false-negative rate. In this context, false negatives are those who have a disorder but are (i) not referred to a clinic or (ii) referred but do not

GENETIC EPIDEMIOLOGY

receive a clinical diagnosis. The generalisability of results will be limited to the degree that these false negatives differ from the probands. Treatment is the most notable factor that differentiates these groups. Multi-stage screening of controls decreases the probability of misclassifying someone with the disorder as a control. Since screened controls are selected for absence of the disorder of interest, they are not representative of the general population, but they are very effective for projects seeking to delineate factors that differentiate controls from cases [4]. Furthermore, unscreened controls frequently have rates of psychopathology and its correlates that are above the population expectation [5–7], thereby obscuring the effects of the variable of interest. Controls should be screened only for the disorder being studied, not for other psychiatric disorders or conditions. When controls are screened for additional disorders, the results can spuriously indicate a familial relationship between the disorder used to select cases and the disorders screened from controls [8]. The selection of controls should satisfy the comparability principles required for meaningful inferences in case–control epidemiological studies [9–12]. It is usually not possible to establish a primary study base with a geographically defined population because the clinics from which probands are selected may serve a broad geographic region that is difficult to delineate. The usual approach establishes a secondary study base defined by the ascertainment source. This limits generalisability and does not produce a representative sample from a geographical population. Nevertheless, it allows for meaningful case–control comparisons if the controls are individuals who could have been cases had they developed the disorder of interest [9–12]. When sampling from a clinic, this requires that, if the control subjects had needed treatment for the disorder, they would have been referred to the clinics that provided the case probands. Instead of establishing a secondary study base, one could match cases and controls on ‘relevant’ variables. One problem here is defining what is and is not ‘relevant’. Age, sex and socioeconomic status are usually considered. Matching should be used cautiously to avoid the ‘matching fallacy’ [13] and ‘overmatching’ [9, 14] because matching on specific variables often unmatches on others [13].

This creates unusual samples, reduces statistical efficiency and biases estimates [12]. These problems are worse when the matching variable is strongly associated with the disorder under study.

3.2.1.2 Assessment of disorder among relatives After selecting case and control probands, the family study compares rates of illness among relatives of cases to rates among relatives of controls. Care must be taken to assess as many relatives as possible. Because psychiatric disorders affect emotions, thinking and interpersonal relationships, nonparticipation may not be random with respect to illness status: ill family members may be more likely to refuse participation than others. If a disorder has a genetic aetiology, then relatives of ill probands should carry a greater risk for the illness than relatives of controls and the risk to relatives of probands should increase with the amount of genes they share in common. First-degree relatives – such as parents, siblings and children – share 50% of their genes, on average, with the proband. They should be at greater risk for the disorder than second-degree relatives (grandparents, uncles, aunts, nephews, nieces and half-siblings) because second-degree relatives share only 25% of their genes with the proband. Family studies rarely have the resources to diagnose second- or third-degree relatives. Table 3.2 displays the familial pattern of risk found in the families of schizophrenic probands, which is similar to that for other psychiatric disorders. These risk figures show that first-degree relatives are at highest risk, followed by second- and then third-degree relatives. In Table 3.2, it is clear that risk for disorder increases with the amount of shared genes; however, the increase in risk is not linear with the increase in biological similarity. Rather, it is exponential, with the individuals most similar to an affected proband (monozygotic (MZ) twins, who are 100% genetically identical) at more than double the risk incurred by individuals with only half their genes in common with an affected proband. These results underscore the complexity of the genetic bases for psychiatric disorders, and imply that gene–gene interactions (epistasis) as well as environmental factors must contribute to their aetiologies. 33

CHAPTER 3 Table 3.2 Rates of schizophrenia among relatives of schizophrenic patients. Type of relative First-degree relatives Parents Children Both parents schizophrenic Brothers and sisters Neither parent schizophrenic One parent schizophrenic Fraternal twins of opposite sex Fraternal twins of same sex Identical twins

Per cent at risk 4.4 12.3 36.6 8.5 8.2 13.8 5.6 12.0 57.7

Second-degree relatives Uncles and aunts Nephews and nieces Grandchildren Half brothers/sisters

2.0 2.2 2.8 3.2

Third-degree relatives First cousins General population

2.9 0.86

Based on Slater and Cowie [15] with the exception of twin data from Shields and Slater [16]. Adapted, with permission from Tsuang et al. [17].

3.2.1.3 Family study vs. family history methods The family history method assesses diagnoses of family members by interviewing only one or several informants per family. In contrast, the family study method determines diagnoses by interviewing each family member [2]. Several excellent structured psychiatric interviews are available but only one was designed specifically for genetic studies: the Diagnostic Interview for Genetic Studies (DIGS; [18, 19]. The main advantage of the family history method is low cost: interviewing a few family members is less costly than interviewing all family members. However, family history data underestimate true rates of many psychiatric disorders. Ideally, diagnoses of subjects should use three sources of information: direct interviews with the subject, family history interviews with informants who are familiar with the subject and medical records when available. All sources of information about a given individual may then be combined into a consensus diagnosis [20, 21]. The direct interview and medical record usually provide more useful information than the family history 34

assessment. In fact, two studies find that diagnoses based on direct interviews alone closely approximated best-estimate diagnoses [20, 21]. However, a diagnosis based only on medical records is often a suitable proxy to the best-estimate diagnosis [20]. The choice between the family history and family study methods requires a tradeoff between data quality and the expense of data collection. The family history method is the method of choice when there are not sufficient data to justify the expense of a family study. It is a good choice for pilot studies. After the family history method demonstrates familiality, the family study is the tool of choice for examining the details of familial transmission and developing reliable estimates of familial risk. When using the family history method, the following should be considered: 1 use the Family Interview for Genetic Studies or some other semistructured method for eliciting the family history; 2 because the family history method has low sensitivity, use less stringent diagnostic criteria than used for direct interviews; 3 use multiple informants for each person to be diagnosed; 4 seek out informants who have had substantial contact with the person to be diagnosed; 5 the method is most valid when the person being diagnosed is ill at the time of interviewing the informant. These ‘rules of thumb’ provide a rough guide for planning a family history study.

3.2.1.4 Caveats We must be cautious in concluding a disorder is caused by genes after we observe that it is familial. Disorders can ‘run in families’ for non-genetic reasons such as shared environmental adversity, viral transmission and social learning. Because the culture and environment shared by family members tends to increase as the degree of relationship decreases, the pattern of risk due to environmental factors may mimic the pattern expected for genetic relationships. Thus, a finding of familial transmission cannot be

GENETIC EPIDEMIOLOGY

unambiguously interpreted. Although family studies are indispensable for establishing the familiality of disorders they cannot establish whether genes or environment mediate that transmission.

3.2.2 What are the relative contributions of genes and environment? Genes, environment and their interaction: these are the ingredients of the pathophysiological brew that engenders psychopathology. To assay these ingredients and determine their relative proportions, we turn to twin and adoption studies [2].

3.2.2.1 Twin studies Identical or MZ twins inherit identical chromosomes and thereby have 100% of their genes in common. In contrast, like siblings, dizygotic (DZ) twins share 50% of their genes. MZ and DZ twins are markedly different with regard to their genetic similarity, but, if twin pairs are reared in the same household then the degree of environmental similarity between MZ twins should be no different than that between DZ twins. The astute reader will note that our comments regarding genetic similarity are facts of inheritance, but our comments about the environment are assumptions. The correctness of these assumptions is key to the valid use of the twin method. Since MZ twins are genetic copies of one another, any differences between a pair of MZ twins are assumed to be due primarily to environmental influences. In contrast, differences between DZ twins could be due to either genetic or environmental influences. Thus, comparing the co-occurrence of a psychiatric disorder in the two types of twins provides information about the relative contributions of genes and environment to the disorder. The co-occurrence of a disorder in both twins is called concordance; if one twin has the disorder and the other does not, the twins are discordant for the disorder. Because we assume the same environmental similarity for both types of twins, a higher concordance rate for MZ compared with DZ twins indicates the influence of genes. We can use pairwise or probandwise concordance rates, depending on the method of sampling the twins. The pairwise concordance rate

is defined as the proportion of twin pairs in which both twins are ill. To compute this, count the number of twin pairs concordant for the disorder and divide the result by the total number of pairs. Use this method when the probability of sampling any specific ill individual is so low that two ill co-twins are never independently sampled as probands. When the sampling probability is higher, use the probandwise concordance rate. Probandwise concordance is the proportion of proband twins that have an ill co-twin. Thus, it is the number of concordant pairs plus the number of concordant pairs in which both the twins are probands, divided by the total number of pairs. Twin data can estimate the ‘heritability’ of a disorder. Heritability measures the degree to which genes influence variability in the manifestation of the disorder (the phenotype). We divide phenotypic variability (Vp ) into two parts: genetic variability (Vg ) and environmental variability (Ve ). This partitioning of phenotypic variability assumes that genetic and environmental factors are statistically independent (i.e. Vp = Vg + Ve ). Heritability in the broad sense (h2 ) is the ratio of genetic and phenotypic variances (i.e. h2 = Vg /Vp ). As these formulas show, a heritability of one indicates that variability in the phenotype is due to genes. A heritability of zero attributes all phenotypic variation to environmental factors. When estimating heritability, diagnostic unreliability increases the estimate of environmental influence. Heritability estimates are context-dependent, and this is reflected by the fact that the heritability estimate accounts for main effects of genetic factors but also gene–environment interactions. The details of methods for calculating heritability are beyond the scope of this chapter. Smith [22] and Plomin et al. [23] provide information about the calculation and interpretation of this measure. If we have data from parents and siblings of twins or indices of the environment, then specialised methods can provide information about gene–environment interaction and gene–environment correlation. An excellent reference for these methods is the book by Neale and Cardon [24]. A major assumption, and often-cited challenge to twin studies, is the ‘equal-environments assumption’. A basic tenet underlying the partitioning of genetic and environmental variance is the assumption that MZ twin-pairs reared together have the same degree 35

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of exposure to similar environmental factors that reared-together DZ twin-pairs have. However, this will be wrong if many more MZ twin-pairs than DZ twin-pairs are treated identically and exposed to the same events. Serious violation of the equalenvironments assumption could result in increased phenotypic similarity among MZ twin-pairs relative to DZ twin-pairs, that is due to environmental – not genetic – similarities between MZ twin-pairs. Thus, a portion of the variance in a phenotype that should be attributed to environmental factors would inadvertently be ascribed to genes, and heritability estimates will be artificially inflated. When MZ twins are reared apart, we have a unique – but rare – opportunity to study the relative importance of genes and environment without having to assume environments are equal. Since MZ twins reared apart do not share a common environment, any phenotypic similarity must be due to genetic factors. However, MZ twins with psychiatric illness are rare, and cases of such twins reared apart are even rarer. Thus, this design cannot be routinely used. A second twin study design uses the children of discordant MZ twins. The logic of this design is straightforward. If a disorder is caused by a genotype combining with environmental factors, then the well member of a discordant MZ twin pair should carry the genotype. Presumably, they did not develop the disorder because they had not been exposed to a relevant environmental cause. If so, then the children of the well twin should have the same risk for the disorder as the children of the ill twin.

3.2.2.2 Adoption studies Children adopted at an early age have a genetic relationship to their biological parents and an environmental relationship to their adopted parents. Thus, adoption studies can determine if biological or adoptive relationships account for the familial transmission of disorders. If genes are important, then the familial transmission of illness should occur in the biological, but not the adoptive family. If culture, social learning or other sources of environmental transmission cause illness, then familial transmission of illness should occur in the adoptive, but not the biological family. 36

There are three major adoption study designs. The parent-as-proband design compares rates of illness in the adopted offspring of parents with and without the disorder. If genetic factors mediate the disorder then rates of illness should be greater in the adopted away children of ill parents compared with the adopted children of well parents. The adoptee-as-proband design starts with ill and well adoptees and examines rates of illness in both biological and adoptive relatives. If the biological relatives of ill adoptees have higher rates of illness than the adoptive relatives of ill adoptees, then a genetic hypothesis is supported. In contrast, if the adoptive relatives show higher rates of illness then an environmental hypothesis gains support. The third design is the cross-fostering design. This approach compares rates of illness for two groups of adoptees: one has well biological parents and is raised by ill adoptive parents and the other has ill biological parents and is raised by well adoptive parents. Higher rates of illness in the former group of adoptees compared with the latter group imply a non-genetic mode of illness transmission. Although they are difficult to execute, adoption studies have provided extensive data for both mood disorders [25–29] and schizophrenia [30–32]. Taken as a group, these studies support the hypothesis that the familial transmission of these disorders is due to genetic, not environmental factors. Adoption studies must be viewed with caution due to potential methodological problems that cloud their interpretation. Adoptees and their families are not representative of the general population. This limits generalisability. Adoptees are at greater risk for psychiatric illness compared with non-adopted children [33, 34]. Although the reasons for this are not clear, this increased risk for psychiatric disorders requires use of an adoptee control group. For example, in the adoptee-as-proband design, the relatives of ill adoptees must be compared with the relatives of well adoptees. Some other control group cannot be used, even if it is matched to the ill adoptee group on demographic measures. It may be difficult to find a sample of adoptees who were all separated from their parents at birth. If the child has lived with a parent for even a short period of time prior to adoption, the biological relationship will have been ‘contaminated’ by environmental

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factors. Some might even argue that the child’s contact with the mother immediately after birth creates a residue of environmental influence that affects subsequent psychopathology. Kety et al. [31, 32] presented a compelling design that deals with this problem. Their method requires a sample of biological paternal half-siblings of ill and well adoptees. Paternal half siblings share a common father yet have different mothers so do not share prenatal, perinatal or neonatal environmental exposure to the same mother. This design rules out confounding by in utero influences, birth traumas and early mothering. In the work of Kety and colleagues, the biological paternal half-siblings of schizophrenic adoptees were at greater risk for schizophrenia than the biological paternal halfsiblings of control adoptees, which bolsters the hypothesis that schizophrenia is caused, at least in part, by genetic factors. There are some environmental correlates of the biological parents that cannot be handled by the paternal half sibling design. Children born to fathers of the lowest social class may share toxic environmental factors such as poor pre- and perinatal care, poor nutrition and an adverse social environment; these may confound the genetic parent–child relationship. Despite these potential confounds and the difficulty of ascertaining appropriate cases and controls, the adoption study remains a valuable tool for disentangling genetic and environmental contributions to the familial aggregation of psychiatric disorders. The problems we note serve to underscore a basic tenet of psychiatric genetic research: any assertion that a disorder is caused by genetic factors must refer not to a single study, but to a series of studies using different paradigms.

3.2.3 What is the mode of transmission? After demonstrating that a disorder is influenced by genetic factors, the next logical task is to determine the mechanism of transmission from parent to child [2]. This information is useful from two perspectives. Showing that the transmission of a disorder corresponds to a known mode of transmission provides clues for subsequent research. For example, if the transmission is clearly due to a single gene, the next step might be linkage analysis, which uses family

psychiatric data and samples of DNA to find mutant genes. If environmental factors are implicated then a search for such factors would be warranted. Moreover, the mode of transmission has implications for genetic counselling. Genetic counselling is the process whereby clinical professionals inform people about either their probability of developing a genetic disorder or that of children they are planning to conceive. Ideally, in the absence of data implicating a particular genetic polymorphism(s), such counselling should be based on risk figures from a known model of genetic transmission. This model can be applied to an individual’s pedigree to determine that individual’s risk for a disorder. Morton et al. [35] demonstrated that the degree of risk predicted depends on the model of transmission. They also found that clinically important errors in risk prediction were made when they used the wrong genetic model to make predictions. A model of familial transmission translates assumptions about genetic and environmental causes into mathematical equations. These equations predict the distribution of a disorder expected in pedigrees or twin pairs. If the pattern of disorder predicted by the model is close to what we observe we say that the model fits the data. In contrast, if the predicted pattern of disorder differs from what is observed we reject the model and seek another. The term segregation analysis is used to describe analyses that assess the mode of disease transmission. The methods we discuss in this section require a good deal of mathematical and statistical expertise to be understood and correctly implemented. In the short space of this chapter we cannot present these mathematical details but instead provide an overview of the different classes of methods used to test hypotheses about genetic and environmental transmission. Several excellent texts, review articles and computer program documentation provide a detailed guide to these methods [1, 36–38].

3.2.3.1 Mathematical modelling of genetic and environmental transmission A genetic model comprises two major components. First, we must describe how the disorder is transmitted. For example, if we believe the disorder is due to a single dominant gene, our model must include the 37

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frequency of the gene in the population. It must also require that the transmission of the gene from parent to child follows the laws of genetic transmission. For example, if a mother carries one pathogenic gene the probability that she transmits this gene to a child must be 50%. Genetic models can specify environmental effects in several ways. In a single gene model we specify the penetrance of each genotype. Penetrance is the probability that each genotype causes disease. If we believe that disease occurs when an environmental event occurs in someone carrying the pathogenic gene, then our model should allow some gene carriers to be well. If other causes for the disease exist, then penetrance exceeds zero for those who do not carry the hypothetical disease gene. Genetic modelling requires a procedure for determining whether model predictions adequately describe the pattern of illness observed in families. One modelling approach attempts to predict rates of illness in various classes of relatives. The pedigree data is reduced to a table of numbers indicating the rate of illness in these classes (e.g. mothers, fathers, brothers, sisters, sons, daughters and more distant relatives). The mathematical model chooses values for the model parameters (e.g. gene frequency and penetrance) that most accurately reproduce the observed rates. The observed and predicted rates can then be compared with a chi-square test to determine if deviations between predicted and observed rates are large enough to warrant rejecting the model. Modelling rates of illness does not capitalise on all the information available in pedigree data. By lumping all families together within one data table, we cannot directly model the transmission of genes from one generation to the next. In contrast, pedigree analysis computes the likelihood of the pattern of illness in each family. For this approach, the analysis uses the status of each person and their relationship to others in the pedigree who are and are not affected. An algorithm then computes the probability, or likelihood, that the assumed model is correct given the pedigree data and the value of model parameters. Those parameter values yielding the most likely model are used as final estimates. With this approach we establish the model’s goodness of fit with a likelihood ratio chi-square test.

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3.2.3.2 Types of transmission models Single gene Mendelian transmission is only one of many mechanisms used to describe family and twin data. We find it useful to classify the genetic mechanisms into three types of models: single major gene, oligogenic and multifactorial polygenic (MFP). The word ‘major’ indicates that one gene can account for most of the genetic transmission of a disorder. Other genes and environmental conditions may play minor roles in modifying the expression of the disease or determining its age of onset. In contrast, an oligogenic model assumes that the combined actions of several genes cause illness. These genes may combine in an additive fashion such that the probability of illness is a function of the number of pathogenic genes. Alternatively, the mechanism may be interactive. For example, three abnormal alleles at different chromosomal locations may be needed for disease to occur. The MFP model proposes that a large, unspecified number of genes and environmental factors combine in an additive fashion to cause disease. The difference between oligogenic and polygenic models is one of degree. The former contain ‘several’ genes (e.g. less than 10) whereas the latter include a ‘large number’ of genes (e.g. [39]). Geneticists originally developed polygenic models to describe quantitative traits such as height and intelligence. By specifying a ‘large number’ of genes, these models could explain how discrete genes could cause traits that were continuously distributed in the population. Since many diseases are qualitative categories – not quantitative dimensions – geneticists developed the concept of liability [40]. Liability describes an unobservable trait: the predisposition to onset with disease. As liability increases so does the probability of disease onset. Alternatively, we might assume that disease occurs when one’s liability crosses a specific threshold. More than one threshold may be placed along the liability continuum, representing varying degrees of severity. Individuals above an upper threshold will develop a severe form of the disorder. Those below the lower threshold may have minor problems or be unaffected, while those whose liability falls between the two thresholds would have an intermediate form of the disorder. The mixed model posits that both MFP and single gene

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components may be involved in disease aetiology. Statistical analysis of the mixed model can determine if either component alone can provide an adequate fit to the data, or if the null hypothesis of no single gene effect and no MFP effect fits best.

3.2.4 Where is the gene (or genes) located? Eventually, psychiatric genetic research leads to questions such as, ‘Where is the gene located?’ This stage of inquiry requires molecular geneticists to provide the methods for tracking the inheritance of these disorders through families [2]. The search for disease genes faces formidable obstacles. Paramount among these is the number of potential disease genes. Each of us has over 20 000 genes. Moreover, only 10% of our chromosomal material (DNA) contains the coding sequences (i.e. instructions) for these genes. The average gene is made up of 3000 bp (the building blocks of DNA). But the entire set of chromosomes (the genome) contains 3 billion bp. Thus, searching for disease genes might seem as difficult as looking for a needle in a haystack. Fortunately, geneticists and statisticians have solved this genetic needle-in-a-haystack problem. Today, there is no question that molecular genetic and statistical technologies can find genes that cause genetic disorders. The list of diseases with known disease genes grows each year. Examples include Huntington’s disease, Alzheimer’s disease, cystic fibrosis, Duchenne’s muscular dystrophy, myotonic dystrophy and familial colon cancer.

3.2.4.1 Background for linkage analysis Linkage analysis is made possible by the ‘crossing over’, which takes place between two homologous chromosomes during meiosis, the process whereby gametes are created. Genetic transmission occurs because we inherit one member of each pair of chromosomes from our mother and one from our father. These inherited chromosomes are not identical to any of the original parental chromosomes. During meiosis, the original chromosomes in a pair cross over each other and exchange portions of their DNA. After multiple crossovers, the resulting

two chromosomes each consist of a new and unique combination of genes. When meiosis is complete, each gamete will contain one chromosome from each of the newly formed pairs. The probability that two genes on the same chromosome recombine during meiosis is a function of their physical distance from one another. This relationship is not linear because recombination events do not occur randomly across the genome, but instead occur at hotspots, leaving other tightly bound segments of the genome relatively intact and heritable as ‘blocks’. We say that two loci on the same chromosome are ‘linked’ when they are so close to one another that crossing over rarely occurs between them. Closely linked genes usually remain together on the same chromosome after meiosis is complete. The greater the distance between loci on the same chromosome, the more likely it is that they will recombine. This biological fact makes it possible to locate genes that are risk factors for disease. Genes on the same chromosome that are very far apart from one another are transmitted independently, as are genes on different chromosomes.

3.2.4.2 Statistical methods for linkage analysis The statistical methods of linkage analysis are beyond the scope of the present chapter, and so are only reviewed in brief. Linkage analysis capitalises on both the occurrence of crossing over and the availability of polymorphic genetic markers. It computes a statistic indicating the probability that the cosegregation of genetic markers and disease within pedigrees exceeds that expected from chance alone. Thus, linkage analysis assesses the association of disease and marker within families.

3.2.4.3 The affected relative pair method The affected relative pair method of linkage analysis evolved from the affected sib-pair method [41, 42]. The original ‘identity by descent’ affected sib-pair method worked with pairs of ill siblings having parents with four different alleles at the marker locus. That is, the father carried two versions of the gene and the mother carried two versions that differed from the father’s. For example, the father might

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have allele A and B and the mother might have C and D. Under the null hypothesis of no linkage, the distribution of alleles shared by siblings at the locus is well defined. For example, consider any of the alleles, say A. The probability that the father transmitted it to the first child is 0.50. The probability of transmitting it to the second child is also 0.50. Therefore, the probability that he transmits A to both children is 0.50 times 0.50 or 0.25. Now assume that the marker locus is close to a disease locus and that the two children have the disease. Because both have the disease gene, both share a segment of DNA that contains the gene and surrounding loci. The size of this segment is not fixed (it depends upon where crossovers occurred). However, the probability that the marker locus is on this segment increases with the proximity of the marker to the disease locus. If the marker and disease loci are contiguous, then children who inherited the disease gene should also have inherited the same allele at the marker locus. We say that the shared marker allele is ‘identical by descent’ to indicate that the alleles observed in the children are copies of the same parental allele. A statistical test was developed to determine whether the observed distribution of marker alleles differed from what was expected in the absence of linkage. The method was later generalised to the case in which the parental marker alleles were not all unique. In this situation we can determine if alleles are ‘identical by state’ but not if they are ‘identical by descent’. Identity by state means that the two alleles are the same but we cannot be certain if they are copies of the same parental gene. For example, suppose the father has allele A and B and the marker locus and the mother has A and C. If two of their children each have allele A at the marker locus then we cannot determine if both received it from the father, both from the mother or one from the mother and the other from the father. The loss of identity by descent information reduces statistical power [43]. The affected relative pair method is a general form of the sibling pair method. It allows all ill relative pairs to be included in the analysis. The major advantage of the affected relative pair method is that it can detect linkage with no a priori knowledge of the genetic and environmental parameters that mediate familial transmission. However, by eliminating 40

information about the mode of inheritance, the method sacrifices some statistical power.

3.2.4.4 The lod score method The lod score method requires knowledge of the mode of inheritance. Although it is possible to estimate the mode of inheritance and test for linkage simultaneously, the usual practice is to test for linkage under an assumed genetic model. We do so by estimating the recombination fraction: the probability that the disease and marker genes will recombine during meiosis. The lower the probability, the greater the likelihood of linkage. Most methods compute a maximum likelihood estimate of the recombination fraction. Then a likelihood ratio test compares the odds of the data occurring given that estimate with the odds of the data if the true recombination fraction is 0.5 (this is our null hypothesis because unlinked loci recombine with a probability of 0.5). This likelihood ratio is an odds ratio comparing the probability that linkage is present with the probability of no linkage. Since we usually examine the base-10 logarithm of the odds ratio, the test statistic is known as the lod score (log of the odds ratio). Lod scores greater than 3 are considered to be evidence in favour of linkage, while lod scores less than −2 constitute evidence against linkage. Thus, a linkage analysis will support the hypothesis of linkage if the odds favouring linkage are 1000 to 1 (i.e. log (1000/1) = 3). The main drawback of the lod score method is that we must specify parameters that describe the mode of genetic transmission. However, there is a way around this problem. Greenberg [44] showed that if we analyse our data several times under different modes of inheritance, the lod score will be greatest for the model closest to the true mode of inheritance. For example, we might choose to examine two dominant models and two recessive models. We might also vary the assumed frequency of the gene in the population. So far, we have been discussing linkage analyses that involve only two loci: one marker locus and one disease locus. Since a disease gene will be surrounded by many potential marker loci, these ‘two point’ analyses will not have optimal power to detect linkage and locate the gene. Multipoint analyses use several markers simultaneously during the linkage

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analysis. Multipoint mapping improves statistical power by using all available marker information in the area of the putative disease locus [45]. Lander [46] proposed ‘interval mapping’ which assesses linkage, not to a single marker, but to an interval flanked by a pair of markers. Xu et al. [47] evaluated interval mapping with statistical simulations. Compared with single point analyses, interval mapping was much more powerful, requiring 30% fewer families to detect linkage. Moreover, interval mapping was more robust to misclassification of penetrances, diagnoses and phenocopies. Although these considerations favour a multipoint approach, the method must be used with caution. Risch and Guiffra [48] showed that, if the mode of transmission is complex, multipoint analyses can spuriously reject linkage. However, they also show that this problem is mitigated when using high estimates of the disease allele frequency. The lod score method has been generalised for the detection of linkage heterogeneity. That is, we can test the null hypothesis that all families are linked in favour of an alternative hypothesis that only a proportion are linked. The lod score criterion of three (LOD3) may not be appropriate for complex genetic diseases like schizophrenia. The LOD3 criterion was originally designed by Morton [49] for Mendelian diseases for which it was reasonable to compute a prior probability of linkage. For non-Mendelian diseases the prior probability is unknown [50, 51]. Morton also assumed that the test was carried out sequentially as pedigrees were collected. Thus, LOD3 does not apply to analyses of fixed sample sizes [50]. The LOD3 criterion must also be adjusted for the effects of testing multiple markers. This includes both the assessment of linkage at multiple loci and the use of multiple markers to assess linkage at a single locus [50, 52, 53]. Guidelines for interpreting linkage results for complex genetic disorders have adjusted the usual 5% probability of false positives since linkage analysis typically consists of multiple statistical tests. Lander and Kruglyak [54] proposed three levels of statistical significance for use in the interpretation of genomewide linkage results. Suggestive linkage would occur by chance once during a genome-wide scan. For the lod score method, the p-value would be less than 0.0017 and for the sib-pair method, p < 0.0007.

Significant linkage refers to a chance event of 0.05 times during a genome-wide scan. For this level of significance, they defined the lod score p < 0.000049 and for the sib-pair method, p < 0.00002. Confirmed linkage refers to the finding of a significant linkage in an initial scan, and independently confirmed in another sample. The use of computer simulation methods to determine the appropriate lod score criterion was demonstrated by Weeks et al. [55]. Briefly, the procedure is as follows. First, the linkage analysis is performed on real data by maximising the lod score over genetic models and phenotype definitions. After a high lod score is found, a second analysis is performed on the same pedigrees. The only difference between the two analyses is that the first analysis uses the real marker data and the second uses simulated marker data. In the second analysis the markers are simulated under the assumption that the disease and marker are not linked. In the simulation, marker genotypes are assigned to subjects whose parents were not studied based on the marker gene frequencies used in the first analysis and the assumption of Hardy–Weinberg equilibrium. Marker genotypes are assigned to other pedigree members by simulating Mendelian laws of transmission on the pedigree. The simulation step is replicated many times and, for each replicate, we record the maximum lod score attained. This provides us with the distribution of maximum lod scores expected under the null hypothesis of no linkage. To set a Type-I error rate of α, we choose the lod score corresponding to the 1 – α point on the cumulative maximum lod score distribution computed by the simulation. To accurately estimate probabilities in the upper tail of the maximum lod score distribution, many replications are necessary.

3.2.5 What are the risk-conferring variants of the genes and what is the mechanism of disease? 3.2.5.1 Association studies Crossing over during meiosis shuffles the parental genes so that the chromosomes we receive from our fathers and mothers are not identical to any of their original chromosomes. Through the generations, 41

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genes are constantly shifting from one chromosome to another. As a result, we should expect no association between alleles of genes on the same chromosome. For example, assume that locus 1 can have allele a or A and locus 2 can have allele b or B. If the two loci are on the same chromosome then the probability that any chromosome contains the pair Ab, P(Ab), should be equal to the probability of A, P(A), times the probability of b, P(b). That is, P(Ab) = P(A) × P(b). Similarly, P(AB) = P(A) × P(b), and so on. Put simply, if we know that a chromosome contains allele A at locus 1, this tells us nothing about the probability of locus 2 containing allele B or b. This random distribution of alleles at different loci on the same chromosome is only partially true. It is an empirical fact that some loci are associated with one another so that P(Ab) = P(A) × P(b) [39]. For example, it may be that chromosomes with allele A at locus 1 are more likely to have allele b at locus 2 than we would expect by chance (i.e. than we would expect from the frequency of allele b in the population). Now, assume that locus 1 is a disease locus and that A is a dominant pathogenic allele. Also assume that locus 2 is a DNA marker locus. If the two loci are associated as indicated above, then people with the disease should be more likely to have marker allele b than people without the disease. This nonrandom association of alleles at different loci is called linkage disequilibrium. One cause of linkage disequilibrium is the fact that the reshuffling of genes on chromosomes depends on genetic distance. If two genes are very close to one another, then they will rarely be separated by crossing over and will usually be transmitted together. Thus, due to very close linkage, the alleles at two loci will tend to be transmitted together. We say ‘tend to’ because eventually crossing over will separate them. Fortunately, the reshuffling of linked genes can take many thousands of years. This means that, theoretically, we should be able to detect associations between diseases and DNA markers if the marker locus is very close to the disease locus. Compared with a linkage study, the design and analysis of an association study is straightforward. We do not require pedigrees with multiple ill members. Samples of unrelated patients and controls will suffice (though family-based association study designs exist, and have their advantages). Instead of a complex 42

linkage analysis, all we need do is compare the rates of marker alleles (or genotypes) in patients and controls with standard statistical tests [39]. Genes within a linked region are candidates for involvement in the phenotype based on their chromosomal location or position (i.e. they are ‘positional candidate genes’). Within a linked region or even in the absence of linkage evidence, a gene may also be a candidate if there is some compelling reason to suspect that the gene influences risk for a given disorder. Association of candidate genes can be evaluated in an independent sample of cases with the disorder and matched control subjects (i.e. in a ‘case–control’ study), or in small family units, where the transmission of variant and normal forms of the gene from parents to offspring can be monitored. In a case–control association study, we simply count the number of each type of allele of a gene, that is found in cases and compare these counts with the allele distribution seen in the control group; this process can also be performed for genotypes. A statistical test is then used to determine if the distribution of alleles observed among cases differs from that seen among controls. If it is different, then we have found evidence for a genetic association with the disorder, where the allele that is over-represented in the group of cases is considered the risk allele. The degree of over-representation of the risk allele in cases relative to controls can be used to derive an odds ratio, which gives a numeric indication of the probability of an affected individual possessing the allele compared the probability of an unaffected individual possessing the allele. Association studies can be performed for alleles or genotypes. In addition, a disorder can be tested for association with a haplotype, which is a pattern of alleles across several markers on the same chromosome (for a description of the International HapMap Project, which is dedicated to cataloguing the haplotype structure of the entire human genome, see http://hapmap.ncbi.nlm .nih.gov/. If linkage disequilibrium, or unusually tight linkage, occurs between the markers in a haplotype, they will typically be inherited together, as no recombination will occur between them. This concept is particularly useful for family-based association studies. In family-based studies, we can use analogous statistics to determine if any difference from the expected equal inheritance of

GENETIC EPIDEMIOLOGY

risk and normal alleles of a gene (or haplotypes within or across several genes) is detected in affected probands who could have received either allele from their parent. In a family-based study, the odds ratio estimates the haplotype relative risk, which represents the increase in the probability of the affected offspring receiving the risk allele (which is presumed to be on the same haplotype as the marker allele) relative to the normal allele. If the odds ratio, relative risk or other effect size attributed to a polymorphism is large enough to attain statistical significance, there are four possible explanations for the result: (i) there is a true association with a causative risk allele; (ii) the associated polymorphism is in linkage disequilibrium (i.e. is in close proximity and usually co-inherited) with the causal variant; (iii) there is some confounding factor that introduces a systematic bias (e.g. population stratification, or background genetic differences between case and control groups) or (iv) the result is due to chance or random error. A disadvantage of association studies is that the DNA marker must either be in the disease gene itself or very close to it. This is in contrast with the linkage method which can detect linkage over relatively large distances. However, unlike linkage analysis, association analysis can detect genes having only a small effect on the susceptibility to illness. Candidate gene association studies are limited by the method used to choose candidates. For a gene to become a positional candidate gene, it must map to a chromosomal region that has been observed to show linkage to the disorder. However, genes with a small but reliable effect on risk may not generate a linkage signal, and thus may never come under study. Selecting genes for association analysis based on their theoretical involvement in the disease process is risky as well. Since our understanding of the biological basis of most psychiatric disorders is far from comprehensive, the pursuit of candidate genes typically progresses incrementally through genes that are expressed within systems widely implicated in the disorder. This is clearly not an optimal process, as the prior probability of selecting the right candidate gene (out of ∼25 000 human genes) and the right polymorphism (out of more than 10 000 000 in the human genome) for analysis is remote. The recent advancement of laboratory and statistical methods

for genome-wide association analysis should allow for a more unbiased examination of association patterns throughout the genome and help resolve this dilemma in coming years [56]. Another limitation of association studies is that they are notoriously difficult to replicate, perhaps owing to their propensity towards false-positive results [57]. The problem of false positive results is exacerbated by the fact that close linkage is not the only cause of disease-marker associations. As discussed above, the frequencies of DNA marker alleles may vary among ethnic groups, cohorts of different ages or other isolated segments of a population. Thus, if case and control groups are not drawn from the same populations and carefully matched on all relevant factors, spurious differences in allele frequencies between groups will emerge due to the population admixture alone [58]. Because it may be difficult to find patient and control groups that are suitably matched for ancestry, genomic control methods have been advocated to account for any imprecision in matching. These methods genotype ancestry-informative markers (i.e. those that differ in frequency across ancestral groups) in addition to those of hypothesised importance in the study, and use the frequencies of these markers in cases and controls to derive an adjustment factor that can be applied to the results pertaining to the hypothesised risk locus. Several investigators have developed tests of linkage disequilibrium that use the parents of ill individuals as controls [59–63], which also circumvents the problems associated with ancestral mis-matching between cases and controls. The transmission disequilibrium test (TDT) uses families having at least one affected offspring and one parent who is heterozygous for the DNA marker to be tested [61]. The TDT compares the number of times heterozygous parents transmit the associated marker allele to affected offspring with the number of times they transmit the other marker allele. If these probabilities differ from what is expected by chance, then we can conclude that linkage disequilibrium exists. Although the TDT solves the problem of ethnicity matching, it still faces the problem of false positives and must be cautiously interpreted in the absence of a credible candidate gene. 43

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Family-based association tests (FBATs) have been developed as extensions to the TDT model, whereby parents or siblings of patients are used as controls. Since each parent transmits only one allele to a child, the allele, that is not transmitted to the child is used as the control allele. The statistical test involves comparisons of the transmitted versus the non-transmitted allele. Because both alleles come from the same parent, there are no differences in ethnicity.

3.3 Psychiatric genetics and psychiatric epidemiology As this chapter shows, psychiatric genetics is a multidisciplinary endeavour. In combines the methodological talents of the epidemiologist, the mathematical proficiency of the statistician and the laboratory wizardry of the molecular geneticist. Although we now look towards molecular genetics and neuroscience to clarify the aetiological and pathophysiological details of psychiatric illness, these are unlikely to succeed without a continued partnership with epidemiology. Many complexities plague psychiatric genetics and many solutions have been proposed in the above referenced articles and others. We have summarised them in 10 key points as follows: 1 Use standardised diagnostic criteria. 2 Define diagnoses that will be included as affected cases before the data collection. 3 Use assessment and diagnostic procedures that minimise false positive diagnoses. 4 Ascertain pedigrees and collect data in a manner that can be reproduced by other investigators;. 5 Collect detailed clinical and demographic data to allow comparisons with other samples and the derivation of quantitative traits. 6 Maintain complete blindness between the psychiatric diagnoses and marker statuses of all subjects. 7 Implement procedures to facilitate the follow-up of pedigree members. 8 Implement procedures to minimise laboratory errors. 9 Use a threshold of statistical significance that takes into account the data analytic issues unique to complex non-Mendelian disorders. 44

10 Allow other investigators access to complete pedigree and clinical information relevant to any publications of linkage results. Psychiatric genetic researchers have a powerful toolbox of methods at their disposal for determining the genetic and environmental causes of mental illnesses. These methods span a wide spectrum, from clinical and behavioural genetic methods to molecular biological assays, reflecting the present status of psychiatric genetics as truly a multidisciplinary field. In addition, new methods such as transcriptomics (i.e. the analysis of gene transcription rates via mRNA quantification) and proteomics (i.e. the analysis of gene translation rates by protein quantification) are pushing the boundaries of what is considered ‘psychiatric genetics’. In a strict sense, these are not genetic techniques and thus may fall under the larger rubric of molecular psychiatry, or even biological psychiatry. However, these techniques examine gene products whose expression is influenced by both genetic and environmental factors, and in this sense, examining such molecules is entirely consistent with the approach of genetic epidemiology, which is to identify both genetic and environmental causes of disease. Despite this progress, the major contributions of psychiatric genetic research to the diagnosis, treatment, prediction and prevention of psychiatric disorders currently remain unrealised. As we have acknowledged throughout the chapter, several limitations of genetic research and its impact on clinical practice must be acknowledged and overcome. Most importantly, the aetiologic heterogeneity of psychiatric disorders must be embraced as the rule rather than the exception. Identifying phenotypic factors that differentiate genetic subtypes will allow future genetic research to derive more reasonable and reliable estimates of familial risk and heritability that are based on the particular features of the affected family and its members. It is nevertheless exciting to visualise the contributions to clinical psychiatry and genetic counselling that await: reduced uncertainty in formulating primary and differential diagnoses; individually tailored pharmacotherapy and disease management; early identification and intervention, leading to better prognosis and ultimately, effective prevention programmes. As technologies improve,

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experimental capacity increases, and computational methods become more efficient, it is expected that the rate of discovery of risk genes for psychiatric disorders will also accelerate. The identification of specific genetic risk factors for psychiatric disorders will then facilitate the identification and quantification of environmental risk factors that interact with these genes to produce illness. A thorough understanding of these determinants of mental illness will allow the considerable promise of the psychiatric genetic approach to be fulfilled.

Acknowledgements Preparation of this article was supported in part by National Institutes of Health GrantsR01DA012846, R01DA018662, R01MH065562, R01MH071912, R21MH075027 and R01MH081861 to Dr. M.T. Tsuang, P50MH081755 and R01MH085521to Dr. S.J. Glatt, and R01DA018659, R01HD053586, R01MH066877, R01MH081803, R13MH059126 and U01MH085518 to Dr. S.V. Faraone, as well as a NARSAD Young Investigator Award to Dr. S.J. Glatt.

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Further reading Thompson, W.D., Orvaschel, H., Prusoff, B.A. and Kidd, K.K. (1982) An evaluation of the family history method for ascertaining psychiatric disorders. Arch. Gen. Psychiatry, 39, 53–58. Mendlewicz, J., Fleiss, J.L., Cataldo, M. and Rainer, J.D. (1975) Accuracy of the family history method in affective illness. Arch. Gen. Psychiatry, 32, 309–314. LaBuda, M.C., Gottesman, I.I. and Pauls, D.L. (1993) Usefulness of twin studies for exploring the etiology of childhood and adolescent psychiatric disorders. Am. J. Med. Genet. Neuropsychiatr. Genet., 48, 47–59. Orvaschel, H., Thompson, W.D., Belanger, A. et al. (1982) Comparison of the family history method to direct interview: factors affecting the diagnosis of depression. J. Affect. Disord., 4, 49–59. Andreasen, N.C. (1986) The family history approach to diagnosis: how useful is it?. Arch. Gen. Psychiatry, 43, 421–429. Gottesman, I.I. and Bertelsen, A. (1989) Confirming unexpressed genotypes for schizophrenia. risks in the offspring

of Fischer’s Danish identical and fraternal discordant twins. Arch. Gen. Psychiatry, 46, 867–872. Silverman, J.M., Breitner, J.C.S., Mohs, R.C. and Davis, K.L. (1986) Reliability of the family history method in genetic studies of Alzheimer’s disease and related dementias. Am. J. Psychiatry, 143 (10), 1279–1282. Ott, J. (1983) Linkage analysis and family classification under heterogeneity. Ann. Hum. Genet., 47, 311–320. Risch, N. (1988) A new statistical test for linkage heterogeneity. Am.J. Hum. Genet., 42, 353–364. Ott, J. (1991) Analysis of Human Genetic Linkage, The Johns Hopkins University Press, Baltimore. Kosten, T.A., Anton, S.F. and Rounsaville, B.J. (1992) Ascertaining psychiatric diagnoses with the family history method in a substance abuse population. J. Psychiatr. Res., 26 (2), 135–147. Elston, R.C. and Namboodiri, K.K. (1977) Family studies of schizophrenia. Bull. Int. Stat. Inst., 47, 683– 697. McGue, M., Gottesman, I.I. and Rao, D.C. (1985) Resolving genetic models for the transmission of schizophrenia. Genet. Epidemiol., 2, 99–110. Risch, N. and Baron, M. (1984) Segregation analysis of schizophrenia and related disorders. Am.J. Hum. Genet., 36, 1039–1059. Faraone, S.V., Kremen, W.S. and Tsuang, M.T. (1990) Genetic transmission of major affective disorders: quantitative models and linkage analyses. Psychol. Bull., 108 (1), 109–127. Goldin, L.R. (1990) The increase in type I error rates in linkage studies when multiple analyses are carried out on the same data: a simulation study. Am. J. Hum. Genet., 47 (3), A180 (abstract). Ott, J. (1990) Genetic linkage and complex diseases: a comment. Genet. Epidemiol., 7, 35–36. Faraone, S.V. and Tsuang, M.T. (1985) Quantitative models of the genetic transmission of schizophrenia. Psychol. Bull., 98, 41–66. Pauls, D.L. and Leckman, J.F. (1986) The inheritance of Gilles De La Tourette’s syndrome and associated behaviors. Evidence for autosomal dominant transmission. N. Engl. J. Med., 315, 993–997. Egeland, J.A., Gerhard, D.S., Pauls, D.L. et al. (1987) Bipolar affective disorders linked to DNA markers on chromosome 11. Nature, 325, 783–787. Kelsoe, J.R., Ginns, E.I., Egeland, J.A. et al. (1989) Reevaluation of the linkage relationship between chromosome 11p loci and the gene for bipolar affective disorder in the old order Amish. Nature, 342, 238–243. Freimer, N.B., Sandkuiji, L.A. and Blower, S.M. (1993) Incorrect specification of marker allele frequencies: effects on linkage analysis. Am. J. Hum. Genet., 52, 1102–1110. Cavalli-Sforza, L.L. and King, M.-C. (1986) Detecting linkage for genetically heterogeneous diseases and detecting

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CHAPTER 3 heterogeneity with linkage data. Am. J. Hum. Genet., 38, 599–616. Ott, J. (1986) The number of families required to detect or exclude linkage heterogeneity. Am. J. Hum. Genet., 39, 159–165. Clerget-Darpoux, F., Babron, M.-C. and Bona¨ıti-Pelli´e, C. (1987) Power and robustness of the linkage homogeneity test in genetic analysis of common disorders. J. Psychiatr. Res., 21 (4), 625–630. Martinez, M.M. and Goldin, L.R. (1989) The detection of linkage and heterogeneity in nuclear families for complex disorders: one versus two major loci. Am. J. Hum. Genet., 44, 552–559. Martinez, M.M. and Goldin, L.R. (1990) Power of the linkage test for a heterogeneous disorder due two independent inherited causes: a simulation study. Genet. Epidemiol., 7, 219–230. Goldin, L.R. and Gershon, E.S. (1988) Power of the affected-sib-pair method for heterogeneous disorders. Genet. Epidemiol., 5, 35–42. Risch, N. (1990) Linkage strategies for genetically complex traits. II. The power of affected relative pairs. Am. J. Hum. Genet., 46, 229–241. McGue, M., Gottesman, I.I. and Rao, D.C. (1983) The transmission of schizophrenia under a multifactorial threshold model. Am. J. Hum. Genet., 35, 1161–1178. Risch, N. (1990) Linkage strategies for genetically complex traits. I. Multilocus models. Am. J. Hum. Genet., 46, 222–228. Risch, N. (1990) Linkage strategies for genetically complex traits. III. The effect of marker polymorphism on analysis of affected relative pairs. Am. J. Hum. Genet., 46, 242–253. Chen, W.J., Faraone, S.V. and Tsuang, M.T. (1992) Linkage studies of schizophrenia: a simulation study of statistical power. Genet. Epidemiol., 9, 123–139. Goldin, L.R. and Martinez, M.M. (1989) The detection of linkage and heterogeneity in nuclear families when unaffected individuals are considered unknown, in Multipoint Mapping and Linkage Based Upon Affected Pedigree Members (eds R.C. Elston, M.A. Spence, S.E. Hodge and J.W. MacCluer), Alan R. Liss, Inc., New York, pp. 195–200. Levinson, D.F. (1993) Linkage information in small family structures: comparison of pedigrees with three to five affected members. Psychiatr. Genet., 3 (1), 45–57. Levinson, D.F. (1993) Power to detect linkage with heterogeneity in samples of small nuclear families. Am. J. Med. Genet., Neuropsychiatr. Genet., 48 (2), 94–102. Boehnke, M. (1986) Estimating the power of a proposed linkage study: a practical computer simulation approach. Am. J. Hum. Genet., 39, 513–527.

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Ploughman, L.M. and Boehnke, M. (1989) Estimating the power of a proposed linkage study for a complex genetic trait. Am. J. Hum. Genet., 44, 543–551. Ott, J. (1989) Computer-simulation methods in human linkage analysis. Proc. Natl. Acad. Sci. USA, 86, 4175–4178. Kendler, K.S., Silberg, J.L., Neale, M.C. et al. (1991) The family history method: whose psychiatric history is measured? Am. J. Psychiatry, 148 (11), 1501–1504. Schweber, M.A. (1985) A possible unitary genetic hypothesis for Alzheimer’s disease and Down’s syndrome. Ann. N. Y. Acad. Sci., 450, 223–238. Korenberg, J., West, R. and Pulst, S. (1988) The amyloid protein precursor gene maps to chromosome 21 subbands q21.15-q21.1. Neurology, 38, 265. Goate, A., Chartier-Harlin, M-C., Mullan, M. et al. (1991) Segregation of a missense mutation in the amyloid precursor protein gene with familial Alzheimer’s disease. Nature, 349, 704–706. Chartier-Harlin, M-C., Crawford, F., Houlden, H. et al. (1991) Early-onset Alzheimer’s disease caused by mutations at codon 717 of the β-amyloid precursor protein gene. Nature, 353, 844–846. Naruse, S., Igarashi, S., Kobayashi, H. et al. (1991) Missense mutation Val-lle in exon 17 of amyloid precursor protein gene in Japanese familial Alzheimer’s disease. Lancet, 337, 978–979. van Duijn, C.M., Hendriks, L., Cruts, M. et al. (1991) Amyloid precursor protein gene mutation in early-onset Alzheimer’s disease. Lancet, 337, 978. Hsu, Y-P.P., Weyler, W., Chen, S. et al. (1988) Structural features of human monoamine oxidase A elucidated from cDNA and peptide sequences. J. Neurochem., 51, 1321–1324. Hsu, Y-P.P., Powell, J.F. and Chen, S. (1988) Molecular genetic studies of MAO genes, in Progress in Catecholamine Research: Part A. Basic and Peripheral Mechanisms (eds A. Dalstrom, H. Belmaker and M. Sandler), Alan Liss, New York, pp. 89–95. Bach, A.W.J., Lan, N.C., Johnson, D.L. et al. (1988) cDNA cloning of human liver monoamine oxidase A and B: molecular basis of differences in enzymatic properties. Proc. Natl. Acad. Sci., 85, 4934–4938. Kobayashi, K., Kurosawa, Y., Fujita, K. and Nagatsu, T. (1989) Human dopamine-beta hydroxylase gene: two mRNA types having different 3’-terminal regions are produced through alternative polyadenylation. Nucleic Acids Res., 17, 1089–1102. Lamouroux, A., Vigny, A., Faucon, B.N. et al. (1987) The primary structure of human dopamine-beta-hydroxylase: insights into the relationship between the soluble and the membrane-bound forms of the enzyme. Eur. Mol. Biol. Organ. J., 6 (13), 3931–3937.

GENETIC EPIDEMIOLOGY Grima, B., Lamouroux, A., Boni, C. et al. (1987) A single human gene encoding multiple tyrosine hydroxylases with different predicted functional characteristics. Nature, 326, 707–711. Bunzow, J.R., Van, T.H., Grandy, D.K. et al. (1988) Cloning and expression of a rat D2 dopamine receptor cDNA. Nature, 336 (6201), 783–787. Grandy, D.K., Litt, M., Allen, L. et al. (1989) The human dopamine D2 receptor gene is located on chromosome 11 at q22-q23 and identifies a TaqI RFLP. Am. J. Hum. Genet., 45, 778–785. Zander, K.J., Fischer, B., Zimmer, R. and Ackenheil, M. (1981) Long-term neuroleptic treatment of chronic schizophrenic patients: clinical and biochemical effects of withdrawal. Psychopharmacology, 73, 43–47. Sunahara, R.K., Niznik, H.B., Weiner, D.M. et al. (1990) Human dopamine D1 receptor encoded by an intronless gene on chromosome 5. Nature, 347, 80–83. Dearry, A., Gingrich, J.A., Falardeau, P. et al. (1990) Molecular cloning and expression of the gene for a human D1 dopamine receptor. Nature, 347, 72–76. Blum, K., Noble, E.P., Sheridan, P.J. et al. (1990) Allelic association of human dopamine D2 receptor gene in alcoholism. J. Am. Med. Assoc., 263 (15), 2055–2060. Gelernter, J., O’Malley, S., Risch, N. et al. (1991) No association between an allele at the D2 dopamine receptor gene (DRD2) and alcoholism. J. Am. Med. Assoc., 266 (13), 1801–1807. Nothen, M.M., Erdmann, J., Korner, J. et al. (1992) Lack of association between dopamine D1 and D2 receptor genes and bipolar affective disorder. Am. J. Psychiatry, 149 (2), 199–201. Schwartz, X.L. and Moises, H.W. (1993) No association between schizophrenia and homozygosity at the D3 dopamine receptor gene. Am. J. Med. Genet., Neuropsychiatr.Genet., 48 (2), 83–86. Conneally, P.M. (1991) Association between the D2 dopamine receptor gene and alcoholism. A continuing controversy. Arch. Gen. Psychiatry, 48, 757–759. Kidd, K.K. (1993) Associations of disease with genetic markers: Deja vu all over again. Am. J. Med. Genet., Neuropsychiatr.Genet., 48 (2), 71–73. Pato, C.N., Macciardi, F., Pato, M.T. et al. (1993) Review of the putative association of dopamine D2 receptor and alcoholism: a meta-analysis. Am. J. Med. Genet., Neuropsychiatr.Genet., 48 (2), 78–82. Crowe, R.R. (1993) Candidate genes in psychiatry: an epidemiological perspective. Am. J. Med. Genet., Neuropsychiatr.Genet., 48 (2), 74–77. Botstein, D., White, R.L., Skolnick, M. and Davis, R.W. (1980) Construction of a genetic linkage map in man using restriction fragment length polymorphisms. Am. J. Hum. Genet., 32 (3), 314–331.

Jeffreys, A.J., Wilson, V. and Thein, S.L. (1985) Hypervariable ‘minisatellite’ regions in human DNA. Nature, 314, 67–73. Marshall, E. (1999) Genomics: drug firms to create public database of genetic mutations. Science, 284, 406–407. Schork, N.J., Fallin, D. and Lanchbury, S. (2000) Single nucleotide polymorphisms and the future of genetic epidemiology. Clin. Genet., 58, 250–264. Wang, J. (2000) From DNA biosensors to gene chips. Nucleic Acids Res., 28, 3011–3016. Sobell, J.L., Heston, L.L. and Sommer, S.S. (1992) Delineation of genetic predisposition to multifactorial disease: a general approach on the threshold of feasibility. Genomics, 12, 1–6. Sommer, S.S., Lind, T.J., Heston, L.J. and Sobell, J.L. (1993) Dopamine D4 receptor variants in unrelated schizophrenic cases and controls. Am. J. Med. Genet., Neuropsychiatr. Genet., 48 (2), 90–93. Gejman, P.V. and Gelernter, J. (1993) Mutational analysis of candidate genes in psychiatric disorders. Am. J. Med. Genet., Neuropsychiatr. Genet., 48(4), 184–191. Murphy, K.C., Jones, A.L. and Owen, M.J. (1999) High rates of schizophrenia in velo-cardio-facial syndrome. Arch. Gen. Psychiatry, 56, 940–945. Buckley, P., O’Callaghan, E., Larkin, C. and Waddington, J.L. (1992) Schizophrenia research: the problem of controls. Biol. Psychiatry, 32, 215–217. Risch, S.C., Lewine, R.J., Jewart, R.D. et al. (1990) Ensuring the normalcy of ‘normal’ volunteers. Am. J. Psychiatry, 147 (5), 682–683. Thaker, G.K., Moran, M., Lahti, A. et al. (1990) Psychiatric morbidity in research volunteers. Arch. Gen. Psychiatry, 47, 980. Weinberg, W. (1925) Methoden und technik der statistik ¨ mit besonderer berucksichtigun der sozialbiologie, in Handbuch der Sozialen Hygiene und Gesundheitsfursorge 1. Grundlagen und Methoden (eds A. ¨ Gottstein, A. Schlossmann and L. Teleky), Verlag von Julius Springer, Berlin, pp. 71–148. Fisher, R.A. (1934) The effect of methods of ascertainment upon the estimation of frequencies. Ann. Eugen., 6, 13–25. McGue, M. and Gottesman, I.I. (1989) Genetic linkage in schizophrenia: perspectives from genetic epidemiology. Schizophr. Bull., 15, 453–464. McGue, M. and Gottesman, I.I. (1991) The genetic epidemiology of schizophrenia and the design of linkage studies. Eur. Arch. Psychiatry Clin. Neurosci., 240, 174–181. Pulver, A.E. and Bale, S.J. (1989) Availability of schizophrenic patients and their families for genetic linkage studies: findings from the Maryland epidemiology sample. Genet. Epidemiol., 6, 671–680.

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CHAPTER 3 Weissman, M.M., Merikangas, K.R., John, K. et al. (1986) Family-genetic studies of psychiatric disorders. Developing technologies. Arch. Gen. Psychiatry, 43 (11), 1104–1116. Bonney, G.E. (1984) On the statistical determination of major gene mechanisms in continuous human traits: regressive models. Am. J. Human Genet., 18, 731–749. Bonney, G.E. (1986) Regressive logistic models for familial disease and other binary traits. Biometrics, 42, 611–625. Bonney, G.E. (1987) Logistic regression for dependent binary observations. Biometrics, 43, 951–973. Borecki, I.B., Lathrop, G.M., Bonney, G.E. et al. (1990) Combined segregation and linkage of genetic hemochromatosis using affection status, serum iron, and HLA. Am. J. Hum. Genet., 47, 542–550. Chase, G.A. and Kramer, M. (1986) The abridged census method as an estimator of lifetime risk. Psychol. Med., 16, 865–871. ¨ Stromgren, E. (1935) Zum ersatz des Weinbergschen ‘abgekurzten verfahrens’ zugleich ein beitrag zur Frage von der Erblichkeit des Erkrankungsalters bei der Schizophrenie. Z. Gesamte Neurol. Psychiatr., 153, 784–797. ¨ Larsson, T. and Sjogren, T. (1954) A methodological, psychiatric and statistical study of a large Swedish rural population. Acta Psychiatr. Neurol. Scand., 89, 40–54. Risch, N. (1983) Estimating morbidity risks with variable age of onset: review of methods and a maximum likelihood approach. Biometrics, 39, 929–939. ¨ Stromgren, E. (1938) Beitrage zur psychiatrischen erblehre auf grund von Untersuchungen an einer Inselbevolkerung. Acta Psychiatr. Neurol. Scand., 19 (Suppl), 1–257. Thompson, W.D. and Weissman, M.M. (1981) Quantifying lifetime risk of psychiatric disorder. J. Psychiatr. Res., 16, 113–126. Cupples, L.A., Risch, N., Farrer, L.A. and Myers, R.H. (1991) Estimation of morbid risk and age at onset with missing information. Am. J. Hum. Genet., 49, 76–87. Chen, W.J., Faraone, S.V. and Tsuang, M.T. (1992) Estimating age at onset distributions: a review of methods and issues. Psychiatr. Genet., 2, 219–238. Heimbuch, R.C., Matthysse, S. and Kidd, K.K. (1980) Estimating age-of-onset distributions for disorders with variable onset. Am. J. Hum. Genet., 32, 564–574. Baron, M., Risch, N. and Mendlewicz, J. (1983) Age at onset in bipolar-related major affective illness: clinical genetic implications. J. Psychiatr. Res., 17, 5–18. Chen, W.J., Faraone, S.V., Orav, E.J. and Tsuang, M.T. (1993) Estimating age at onset distributions: The bias from prevalent cases and its impact on risk estimation. Genet. Epidemiol., 10, 43–60. Sturt, E. (1985) Estimating morbidity risks with variable age of onset (correspondence). Biometrics, 41, 311–313.

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Lee, E.L. (1980) Statistical Methods for Survival Data Analysis, Lifetime Learning, Belmont. Faraone, S.V., Biederman, J., Krifcher, B. et al. (1993) Evidence for independent transmission in families for Attention Deficit Hyperactivity Disorder (ADHD) and learning disability: results from a family-genetic study of ADHD. Am. J. Psychiatry, 150, 891–895. Kaplan, E.L. and Meier, P. (1958) Nonparametric estimation from incomplete observations. Am. Stat. Assoc. J., 53, 457–481. Breslow, N. and Crowley, J. (1974) A large sample study of the life table and product limit estimates under random censorship. Ann. Stat., 2, 437–453. Lewis, S.W., Reveley, A.M., Reveley, M.A. et al. (1987) The familial/sporadic distinction as a strategy in schizophrenia research. Br. J. Psychiatry, 151, 306–313. Kendler, K.S. and Hays, P. (1982) Familial and sporadic schizophrenia: a symptomatic, prognostic and EEG comparison. Am. J. Psychiatry, 139, 1557–1562. Lyons, M.J., Faraone, S.V., Kremen, W.S. and Tsuang, M.T. (1989) Familial and sporadic schizophrenia: a simulation study of statistical power. Schizophr. Res., 2, 345–353. Kendler, K.S. (1987) Sporadic versus familial classification given etiologic heterogeneity: sensitivity, specificity, and positive and negative predictive power. Genet. Epidemiol., 4, 313–330. Eaves, L.J., Kendler, K.S. and Schulz, S.C. (1986) The familial sporadic classification: Its power for the resolution of genetic and environmental etiological factors. J. Psychiatr. Res., 20, 115–130. Lyons, M.J., Kremen, W.S., Tsuang, M.T. and Faraone, S.V. (1989) Investigating putative genetic and environmental forms of schizophrenia: Methods and findings. Int. Rev. Psychiatry, 1, 259–276. Erlenmeyer-Kimling, L. (1975) A prospective study of children at risk for schizophrenia: methodological considerations and some preliminary findings, in Life History Research in Psychopathology (eds R. Wirt, G. Winokur and M. Ross), University of Minnesota Press, Minneapolis, pp. 22–46. Mednick, S.A., Mura, E., Schulsinger, F. and Mednick, B. (1971) Perinatal conditions and infant development in children with schizophrenic parents. Soc. Biol. (Suppl. 18), 103. Fish, B., Marcus, J., Hans, S.L. et al. (1992) Infants at risk for schizophrenia: sequelae of a genetic neurointegrative defect. A review and replication analysis of pandysmaturation in the Jerusalem infant development study. Arch. Gen. Psychiatry, 49, 221–235. Biederman, J., Rosenbaum, J.F., Bolduc, E.A. et al. (1991) A high risk study of young children of parents with panic disorder and agoraphobia with and without comorbid major depression. Psychiatry Res., 37, 333–348.

GENETIC EPIDEMIOLOGY Orvaschel, H. (1990) Early onset psychiatric disorder in high risk children and increased familial morbidity. J. Am. Acad. Child Adolesc. Psychiatry, 29 (2), 184–188. Tsuang, M.T., Faraone, S.V. and Lyons, M.J. (1993) Advances in psychiatric genetics, in International Review of Psychiatry, vol. 1 (eds J.A. Costae Silva, C.C. Nadelson, N.C. Andreasen and M. Sato), American Psychiatric Press, Washington, DC, pp. 395–440. Tsuang, M.T., Gilbertson, M.W. and Faraone, S.V. (1991) Genetic transmission of negative and positive symptoms in the biological relatives of schizophrenics, in Positive vs. Negative Schizophrenia (eds A. Marneros, M.T. Tsuang and N. Andreasen), Springer-Verlag, New York, pp. 265–291. Morton, N.E., Rao, D.C. and Lalouel, J.-M. (1983) Methods in Genetic Epidemiology, Karger, New York. Sorant, A.J.M. and Elston, R.C. (1989) Segregation analysis of a truncated (censored) trait with logistic P.D.F. (REGTL version 1.0), in Statistical Analysis for Genetic Epidemiology (eds J.E. Bailey-Wilson and R.C. Elston), Department of Biometry and Genetics, LSU Medical Center, New Orleans. Morton, N.E. and MacLean, C.J. (1974) Analysis of family resemblance. III. Complex segregation analysis of quantitative traits. Am. J. Hum. Genet., 26, 489–503. Iselius, L. and Morton, N.E. (1991) Transmission probabilities are not correctly implemented in the computer program POINTER. Am. J. Hum. Genet., 49 (459), 459. Sorant, A.J.M. and Elston, R.C. (1989) A subroutine package for function maximization (A users guide to MAXFUN version 5.0), in Statistical Analysis for Genetic Epidemiology (eds J.E. Bailey-Wilson and R.C. Elston), Department of Biometry and Genetics, LSU Medical Center, New Orleans. Akaike, H. (1974) A new look at statistical model identification. IEEE Trans. Autom. Control, AC-19 (6), 716–723. DeLisi, L.E., Dauphinais, I.D. and Hauser, P. (1989) Gender differences in the brain: are they relevant to the pathogenesis of schizophrenia? Comp. Psychiatry, 30 (3), 197–208. Goldstein, J.M., Tsuang, M.T. and Faraone, S.V. (1989) Gender and schizophrenia: implications for understanding the heterogeneity of the illness. Psychiatry Res., 28 (3), 243–253. Faraone, S.V., Biederman, J., Keenan, K. and Tsuang, M.T. (1991) A family-genetic study of girls with DSM-III attention deficit disorder. Am. J. Psychiatry, 148 (1), 112–117. Pauls, D.L. (1979) Sex effect on the risk of mental retardation. Behav. Genet., 9 (4), 289–295.

Harris, T., Surtees, P. and Bancroft, J. (1991) Is sex necessarily a risk factor to depression? Br. J. Psychiatry, 158, 708–712. Cloninger, C.R., Christiansen, K.O., Reich, T. and Gottesman, I.I. (1978) Implications of sex differences in the prevalences of antisocial personality, alcoholism, and criminality for familial transmission. Arch. Gen. Psychiatry, 35, 941–951. Berney, T.P. (1989) Fragile X syndrome and disorders of the sex chromosome. Curr. Opin. Psychiatry, 2, 593–598. Khoury, M.J., Beaty, T.H. and Cohen, B.H. (1993) Fundamentals of Genetic Epidemiology, Oxford University Press, New York. Ottman, R. (1990) An epidemiologic approach to gene–environment interaction. Genet. Epidemiol., 7, 177–185. Fischer, M. (1971) Psychosis in the offspring of schizophrenic monozygotic twins and their normal co-twins. Br. J. Psychiatry, 118, 43–52. Merikangas, K.R., Spence, A. and Kupfer, D.J. (1989) Linkage studies of bipolar disorder: methodologic and analytic issues. Report of MacArthur foundation workshop on linkage and clinical features in affective disorders. Arch. Gen. Psychiatry, 46, 1137–1141. Ott, J. (1990) Invited editorial: cutting a Gordian knot in the linkage analysis of complex human traits. Am. J. Hum. Genet., 46, 219–221. Risch, N. (1990) Genetic linkage and complex diseases, with special reference to psychiatric disorders. Genet. Epidemiol., 7, 3–7. Weeks, D.E., Brzustowicz, L., Squires-Wheeler, E. et al. (1990) Report of a workshop on genetic linkage studies in schizophrenia. Schizophr. Bull., 16 (4), 673–686. Pato, C.N., Lander, E.S. and Schulz, S.C. (1989) Prospects for the genetic analysis of schizophrenia. Schizophr. Bull., 15 (3), 365–372. Faraone, S.V. and Santangelo, S. (1992) Methods in genetic epidemiology, in Research Designs and Methods in Psychiatry (eds M. Fava and J.F. Rosenbaum), Elsevier, Amsterdam, pp. 87–105. Andreasen, N.C., Endicott, J., Spitzer, R.L. and Winokur, G. (1977) The family history method using diagnostic criteria. Reliability and validity. Arch. Gen. Psychiatry, 34, 1229–1235. NIMH Genetics Initiative (1992) Family Interview for Genetic Studies, National Institute of Mental Health, Rockville.

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4

Examining gene–environment interplay in psychiatric disorders Judith Allardyce1 and Jim van Os1,2 1 Maastricht University Medical Centre, School of Mental Health and Neuroscience, Department of Psychiatry and Neuropsychology, South Limburg Mental Health Research and Teaching Network, Maastricht, The Netherlands 2 King’s College, King’s Health Partners, Department of Psychosis Studies, Institute of Psychiatry, London, UK

4.1 Introduction Epidemiologists have traditionally studied the distribution and determinants of health related states as a function of environmental exposures; for example stressful life events, pregnancy and birth complications, minority status, urban environments and cannabis use. The aim has been to identify environmental risk factors that are causal and potentially modifiable. In contrast, classical psychiatric genetics has tended to focus on gene mapping to identify single susceptibility or candidate genes for a particular disorder, or on statistical modelling techniques that aim to quantify heritability. Genetic methodologies assume that genetic determinants are true signals while environmental effects are noise, which should be controlled for where possible, while studies examining only environmental risk factors, do not take account of the possibility that exposure and outcome may share a genetic liability. Over the past few decades, it has become increasingly clear that the identification of specific genes and environmental risk factors will be greatly aided by integrating the respective fields of epidemiology and genetics into the new discipline of genetic epidemiology, which considers the joint actions of genetic and environmental factors in causing disease, within human populations and

the pattern of inheritance in families. Family studies have been the basic approach used by genetic epidemiologists but classical epidemiological designs such as case–control and cohort studies are considered useful in many situations [1–4]. Genetic epidemiology considers both environmental and genetic risk factors – and their interactions – with potential parity, by extending the conceptualisation of epidemiological exposures to include genetic factors and family relationships [5, 6]. This joint approach aims to unravel the pathway from genotype to phenotype by trying to understand how an individual’s genetic makeup modifies their susceptibility to environmental exposures or modifies their level (dose) of causal environmental exposures and explores ways in which the physical and social structure of the environment may exacerbate genetic risk. In actual fact the best evidence that there are non-genetic causal factors in the expression of psychiatric disorders comes from the classical twin studies which demonstrate concordance rates for monozygotic twins of between 50 and 70% for schizophrenia or mood disorders, though of course it is also quite probable that (partial) genetic mechanisms such as epigenetic effects, stochastic factors or mitochondrial inheritance could contribute to this discordance, conflating the ‘environmental’ contribution estimated [7–9]. Similarly, standard

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

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heritability scores are confounded, in that they do not discriminate between ‘purely’ genetic determinants and gene–environment correlation (genetic mediation of the level of environmental exposures) and interaction (genetic mediation of the susceptibility of a causal environmental exposure). The high proportion of monozygotic pairs that remain unaffected, certainly points towards an environmental influence in the aetiology of these disorders [10, 11].

4.2 The process of genetic epidemiology The identification of causal factors in disease onset generally follows a series of logical steps or questions. This is the process or chain of genetic epidemiological research [2]. First, there is a systematic analysis of the rates of disease, comparing and contrasting rates in populations over time, between place and within different subgroups, for example; in people who have migrated, or between people of different social economic class and age/gender variations can all provide clues to putative genetic and environmental casual factors. The second question asks whether the disorder tends to run in families (do the relatives of patients with a disorder have higher rates of a specified disorder, greater than would be expected by chance alone?) Once a familial pattern is identified the risk to relatives is examined for correlation to closeness (degree) of the relationship, that is first degree relatives (parents, siblings and children) who share 50% of their genes on average with the patient should have a higher risk for the disorder, than second degree relatives who share on average only 25% of their genes with the affected person. The family study is a robust design, in many cases providing the initial clue that a disorder has a genetic component; however we have to be cautious in our interpretation of such familiarity as there are always alternative non-genetic explanations for family clustering, such as shared environment, social learning and viral causations, to name but a few. The third question asks what type of genetic transmission is occurring, is the familiar pattern compatible with one or more major genes or more suggestive of an oligogenic, polygenetic transmission 54

or shared environmental factors? Single major gene models propose that one gene accounts for most of the genetic transmission while other genes and environmental exposures play only a minor role in modifying the expression of the disorder or determining its age of onset. Oligogenic models assume that a few genes (e.g., less than 10) combine to cause the disorder. This joint effect can be additive, that is the likelihood of developing the disorder is simply the linear function of a number of genes or alternatively the mechanism may be interactive or a combination of the two models. The multifactorial–polygenetic model posits that an unspecified number of genes, perhaps running into the hundreds plus environmental factors act additively or interactively to increase risk of a disorder. Associated with the polygenetic model of disease is the concept of genetic liability, which is a latent trait that predisposes an individual to a particular disorder; the functional form of this may be a continuous linear association or a threshold form when disease occurs once a liability threshold has been crossed. The polygenetic model assumes that liability is normally distributed in the population. The fourth question asks where the genes for the disorder are located. This uses linkage analyses, a methodology examining family pedigrees (multiple case families) or affected sib pairs, using polymorphic markers of known chromosomal location in blood samples taken from the patent and their family. Linkage analyses establish whether markers are transmitted through the pedigree in a manner that parallels disease transmission (cotransmission/cosegregation) so that the general chromosomal location of the susceptibility gene can be identified. This process of gene mapping often begins by examining an array of widely spaced markers positioned across the whole genome, the search region narrowing down as information accrues and is later augmented with fine tuning techniques such as linkage disequilibrium (LD) mapping, which exploits the fact that common variants which are located close together on a chromosome (<= 10 000 bp) are likely to be transmitted together, that is are in LD. Therefore if one variant increases the risk of a common disorder (i.e., a direct association), genetic variants in LD with it will also be associated (indirectly) with the disorder. It remains unclear how effective linkage studies have been in

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

identifying candidate genes for psychiatric disorders. Statistically significant linkage has been found but replication has been inconsistent presumably due to gene variants having small and heterogeneous effects. However, there is some support for its effectiveness in autistic spectrum disorder and bipolar disorder [12, 13]. If the polygenetic model is a good approximation to the genetic architecture of common psychiatric disorders (this is not fully accepted) , then it is likely the genes involved will be of small effect, therefore requiring very large numbers of affected families to make such studies practical [14]. The fifth question therefore, asks how strongly the identified genes are related to the disorder. Association studies have the potential to identify causal genes of small effect in realistically sized samples even in unrelated subjects. By comparing genotypes at candidate loci in cases and controls (family and population-based case–control studies) the strength of the relationship can be estimated. The main problem in designing association studies is that there is still no clearly defined understanding of the pathogenesis of major psychiatric disorders and so myriad potential genes could theoretically be involved. Candidate gene hypotheses for most psychiatric disorders have been extrapolated from the pharmacological actions of drugs used in their management, focusing particularly on functional polymorphisms implicated in the dopaminergic and serotonergic pathways [15–17]. Association studies are susceptible to type 1 errors, as low prior probability from multiple testing of multiple single gene variants makes it difficult to sort out true, from false positive associations [18, 19] a problem that will be even more problematic in genome-wide association studies (GWASs), which investigate a million genetic markers or more, at the same time [20]. Such major methodological problems have resulted in poor reproducibility of findings from association studies, as samples vary in their demographic profiles, confounder backgrounds and comorbidity characteristics. This is especially problematic if the genetic variant only increases risk of disorder under certain specific environmental conditions, that is: if there is gene–environment interaction (GxE). If this is the case, harnessing such heterogeneity in the sense of exploiting any GxE may aid the identification of susceptibility genes. The final

question in the epidemiological process therefore asks about the character of the genetic effect and includes examining interplay with environmental factors and measuring the frequency of high risk variations within the population. (See Text Box 4.1.)

4.3 Gene–environment interplay takes different forms There are a variety of biologically plausible mechanisms by which genes and the environment can co-influence onset of disease. These are: gene– environmental correlation (GEr) reflecting genetically influenced differences in exposure to particular environmental factors, GxE (co-action) referring to genetic influenced differences in susceptibility to particular environments and epigenetic mechanisms.

4.4 Gene–environment correlation Genetic expression has traditionally been considered a process taking place entirely within the constraints of the physiological milieu of an individual and the associated corollary of this conceptualisation is that any association between the individual and their external environment will be unidirectional, that is genes will have no influence on environmental exposures. The last few decades has seen a revision of this view, as it has became clear that some genes have an impact on their external environmental setting through behaviours which are, at least partly genetically determined, that is bidirectional relationship between genes and environment is probable [21]. Twin studies suggest genetic factors operate through pathways external to the person, influencing exposure to a range of environmental risk factors such as stressful life events, poor social support and marital relationship quality [22–24]. That individuals have an active role in the selection, modification and construction of their environmental milieu is now widely accepted by behavioural geneticists and evolutionary biologists. Some environmental exposures may indeed be heritable, a phenomenon referred to in evolutionary biology as the extended phenotype [25]. It has been shown in animal behavioural studies that the way animals modify their physical environment, 55

CHAPTER 4

Box 4.1 The process to determine the joint gene–environmental interplay influencing the risk for psychiatric disorders.

• generation of hypotheses about the relative contribution of putative genetic and environmental risk factors

Descriptive Epidemiology

• family history studies • twin & adoption studies

Determine whether there is familiar aggregation

• What is the genetic model of transmission? • single gene • few genes • poly gene

Segregation analyses

Locate risk gene (genes) main effects / interaction using Linkage & association studies

methods employed to measure genetic exposure

Study Design

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• Proxy (surrogate) indicators of genetic risk • family history • intermediate phenotypes • sibling correlations • Molecular genotyping • Candidate gene approach • GEWIS

• Cohort • (nested case control) • Case Control • Family member as control • General population control • Family Study • Sib pair analysis • case-parent trios • multi generational pedigrees

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

for example how they build burrows, dams and webs is not randomly distributed but in part, involves heritable traits. Furthermore in social animals such as rodents, the provision and development of different parental nurturing behaviours (e.g., feeding routines) is partly predicted by variation in their genetics. Furthermore, selection experiments find genes to be associated with aggressive traits which lead the rodent to experience a different social milieu, compared to that of their less aggressive counterparts [24]. GEr can be both causal (Figure 4.1) and noncausal (Figure 4.2) [26]. Non-causal GEr occurs when the health outcome and the environmental factor under study share a genetic liability, but the environmental factor does not have a real causal relationship to the outcome, that is the observed environmental health outcome association is confounded by genotype. Behavioural contamination may also result in GEr when genetic/individual factors influence how a person feels or perceives a situation, which will be reflected on how they report environmental exposures. This information bias will be especially problematic when environmental exposure is collected retrospectively. Causal GEr occurs when there is (at least in part) a genetically mediated variation in causal environmental exposure profiles, that is part of a causal pathway. Genotype is unlikely to code directly for specific environmental exposures, but is more likely to act indirectly, through factors such as behaviour and personality; most studies to date have looked at dimensions of neurotism, extraversion and openness to experience, with shared genetic influences evident in studies examining neurotism scores and parenting and neurotism and stressful life events [26, 27].

Gene

O

BS

ER

VE

D

AS

SO

CI

AT

IO

N

LEVEL OF CAUSAL ENVIRONMENTAL FACTOR

PSYCHIATRIC DISORDER

Fig 4.1 Casual: gene–environment correlation.

Gene

True causal relationship

ENVIRONMENTAL FACTOR CONFOUNDED ASSOCIATION

Fig 4.2

PSYCHIATRIC DISORDER

Non-casual gene–environment correlation.

Three different GEr mechanisms have been described. Passive GEr occurs as most children inherit their genetic characteristics and early rearing environment from the same biological parents, for example parental maltreatment is associated with childhood conduct disorder; however, antisocial behaviour has been demonstrated to be moderately heritable and parents with such traits are more likely to abuse their children, therefore the maltreatment may be indicative of genetic risk transmitted by the parent to the child rather than a true environmental risk factor for conduct disorder [21]. Evocative (reactive) GEr refers to the impact an individual’s behaviour has on their social environment, especially the reaction of others to their behaviour, such that a shy person and a gregarious person evoke different responses in the same social setting. An association between marital difficulties and depression has been demonstrated; however, this relationship may reflect the conflicts that arise from interacting with someone who is depressed, rather than marital difficulties causing depression per se [21]. Selective (active) GEr occurs when an individual’s genetically mediated personality traits and behaviours influence the environmental ‘niches’ they select to live their life in. Kenneth and Baker [28] have recently carried out a systematic review of human studies examining the heritability (the proportion of individual differences for a trait in a particular population that results from inter-individual genetic differences) of environmental exposures [28]. They identified 55 independent papers reporting on general and specific stressful life events, parenting, family environment, social 57

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support, peer interactions and marital quality and found weighted heritability estimates ranging from 7 to 39%. This review suggests that all aspects of the environment studied in the literature to date, have a significant genetic influence but with small to moderate effect sizes. The review suggests that stressful life events which are more dependent on an individual’s own behaviour (e.g., divorce) are more heritable than events that are out with the control of the individual (e.g., death of a loved one). It found parenting behaviours reflecting positive emotional quality of the parent-child relationship were more heritable than parenting behaviour related to discipline styles. Importantly, it seems that the genetic makeup from all parties in a dynamic relationship contribute equally to the quality of the environmental experience. For example, in the child–parent relationship the genes from the parent seem to impact as much as the genes in the child, therefore it is possible that risk of psychiatric disorders may be mediated in part through self selection into pathogenic environment.

4.5 Gene–environment interaction GxE is defined as genetically moderated variation in the susceptibility to environmental exposures (Figure 4.3). There is biological plausibility and face validity in suspecting GxE to be relatively common in nature [29, 30]. From evolutionary theory, we know that it is gene–environmental interplay that drives an organism’s adaptation and evolution over subsequent generations. Furthermore, GxE mechanisms could help explain the ubiquitous heterogeneity of susceptibility to environmental hazards and opportunities seen between individuals [31]. Biological GxE is an explanatory model for causal mechanism and will require experimental validation as each element along the causal pathways emerges [32]. Some commentators have highlighted the distinction between biological and statistical interaction [33] emphasising that it is a core biological construct, best understood by the iterative delineation of specific mechanisms along causal pathways [34]. While this makes theoretical sense, in human epidemiological studies the 58

Gene Di

Direct effect may or may not be present

re

ct

ef

fe

SUSCEPTIBILITY ENVIRONMENTAL FACTOR

ct

PSYCHIATRIC DISORDER

Fig 4.3 Gene–environment interaction.

only way biological synergism can be demonstrated is via inference from statistical interactions. The current conceptual model for multi-factorial disease is the sufficient-component cause framework. This posits that a given disorder can have more than one sufficient causal mechanism, and every causal mechanism involves the joint action of multiple component causes, therefore any identified risk factor, be it genetic or environmental, will be neither necessary nor sufficient to produce the disorder. Inherent in this model is the concept of interaction. If a component cause is not sufficient, then it must coparticipate with other factors to produce disease [34]. Such joint effect mechanisms, sometimes known as sufficient causal pies, do not characterise a specific disease model or require component factors to act at the same time. It is also probable that specific component causes play a role in more than one sufficient causal mechanism. Biological synergism/interaction is therefore defined when two risk factors are components of the same sufficient cause [35]. If the two factors are part of different sufficient causes, their combined effects on risk will simply be the sum of their effects (additive).

4.6 Measurement of genotype, environmental exposure and pathological phenotype 4.6.1 Measurement of genetic variants There are three different approaches to measuring the genetic component in GxE studies; (i) The hypothesis-driven molecular candidate gene approach; (ii) Molecular whole genomic scanning approaches, which have no a priori hypothesis

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

but hunt for genes; (iii) Omnibus approaches: using surrogate (proxy) variables of genetic risk. The first two approaches (to date) have used DNA array, though expression arrays (messenger RNA and non coding RNA) and proteome analysis may be utilised in the future. The common DNA sequence markers used in GxE studies are SNPs (single nucleotide polymorphisms) CNVs (copy number variants) and SSRs (simple sequence repeats). While genome–environment wide interaction studies (GEWISs) are being proposed, to date population based GxE studies have used the candidate gene approach. The selection of the candidate genes should have a biologically plausible hypothesis. Information regarding the function of candidate genes and its validated SNPs can be found in genetic information websites [35]. Neale and Sham [36] suggest selecting gene variants using criteria based on their function in order of priority: amino acid change, promoter polymorphism; association with potential splice sites, synonymous coding regions variation and non coding (intronic) variants. In addition, they suggest using multiple markers spanning the length of the candidate gene to ensure all its regions are investigated [36]. However, to avoid redundancy when selecting multiple SNPs, LD can be exploited (i.e., dependence of loci usually in close proximity on the gene). This can be measured by inferring haplotypes (specific set of alleles at linked genetic loci). If a haplotype is identified then it is often possible to identify a single ‘tag’ marker, which will capture most of the variation across that region of the gene [37] so reducing the number of markers required for full coverage. Molecular genotyping is prone to genotyping errors, which can lead to loss of statistical power, therefore it is important to quality control genetic analyses [38]. Omnibus approaches using proxy or surrogate measures of genetic exposure such as family history or intermediate (endo)phenotypes (heritable biomarker, lying along the causal pathway from gene to disorder, but at a more proximal position to the gene, than the manifest symptoms) [39] are useful approaches as they potentially allow the combined genetic contribution to be quantified, including all unspecified GxG and GxE, which may contribute to differential susceptibility for

environmental exposures. The drawback of omnibus models is non-differential information bias from false negative misclassification of the genetic risk.

4.6.2 Measurement of environmental exposures Ideally the environmental exposures used in GxE should be an evidenced causal factor. This is a problem for GxE studies in psychiatric disorders as very few of the environmental risk factors for common psychiatric disorders meet this criterion. The environmental exposures should be measured accurately and if possible be multifaceted and include: timing (specific developmental stages), duration (discrete interval dosing or continuous exposures) and intensity (e.g., cannabis can be ingested in different forms with different tetrahydrocannabinol levels), in order to avoid misclassification which can significantly bias main effect estimates as well as interaction effects. To date, studies have tended to employ dichotomous environmental exposures, for example urban versus non-urban environment. However, the categorisation of continuous exposures, results in substantial loss of information and power, therefore it is advantageous to use the continuous measure. Possible exceptions are when there is a priori evidence to support a possible threshold model of association between the exposure and disorder. For example, the relationship between stressful life events and increased risk of depression, only holds for severe contextual threats [32, 40]. Methodologies which capture the cumulative nature of many of the ongoing chronic environmental exposures for example momentary assessment technologies, are likely to be useful [41]. Specific methodological issues around the measurement of environmental exposures are discussed in the study design section. Psychiatric epidemiological studies in the 1980– 1990s focused primarily on environmental exposures at the level of the individual (e.g., obstetric complications, an individual’s cannabis use). Over the next decade, researchers will try and characterise environmental exposures not just at the individual (and molecular) level but across a hierarchy of systemic complexity, including the micro shared environments (e.g., shared by families); neighbourhood composition and macro societal levels factors [42, 43]. 59

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4.6.3 Measurement of the pathological phenotype (disorder) Psychiatric disorders are categorical constructs and therefore it is attractive to treat them as dichotomous outcomes in GxE analyses. However, psychopathology can also be conceptualised as continuous latent variables (dimensions), the merits of which have been highly debated for depression and psychotic disorders [44, 45]. In future studies, it may be appropriate to use a continuous pathological outcome measure which prevents substantial loss of variability and power if there is no evidence of a bimodal distribution in the psychopathological outcome in the population under study. Another approach to the measurement of pathological outcome that may yield more consistent estimates of GxE is the use of phenotypes that are more proximal to the underlying pathophysiological mechanisms, such as intermediate (endo)phenotypes. For example, while initial report on the role of the hypothesised interaction between variations in the gene encoding the serotonin transporter and life stress in depression generated much interest, recent meta-analysis of this association concluded that there was no evidence to support GxE [46]. A possible explanation for this finding may be that behavioural measures of life events and depression introduce more error than proximal biological measures such as amygdala activation in response to experimental emotional stimuli, where meta-analysis of moderation by the same serotonin transporter polymorphism does suggest GxE [47].

of E and G according to whether the factor is present or absent. • r(E) the risk in the population exposed to the environmental factor only. • r(G) the risk in the population exposed to the genetic influence only. • r(GE) the risk in the population exposed to both the genotype and environmental risk factor. • r(00) the risk in the population exposed to neither exposure. If no interaction of G and E is present (that is, conditional independence) then the effect of G on the disease risk is the same across strata defined by E; however if the risk of disease varies across strata of E, then interaction is said to exist. Under strict statistical definitions whether or not an interaction exists will depend on the scale of the measurement. If risks are measured on the additive scale, so the effect of a risk factor is expressed as a risk difference (attributable risk), for example r(G) is 0.25 and r(00) is 0.10, then the effect of G is 0.25 – 0.10 = 0.15, the effect of G can then be expressed as r(G) – r(00), the effect associated with E as r(E) – r(00) and the effect associated with the joint GE exposure as r(GE) – r(00). The expected patterns of risk difference and relative risk with and without interaction would therefore be [48, 49] Model of joint action No interaction

4.7 Models of GxE To illustrate how GxE are modelled we will use the (overly) simple situation where all the three variables are dichotomous, and assume that the genetic and environmental factors increase the risk for disorder rather than reduce it. The underlying principles would be the same for protective effects, though some statistical extensions may be necessary. E is an environmental risk factor, G is a single gene variant risk factor, disease risk is the proportion of individuals who develop the pathology denoted as r. This situation results in four possible combinations 60

Synergistic action

Risk pattern r(GE) − r(G) = r(E) − r(00) r(GE) − r(G) > r(E) − r(00)

Relative risk (RR) pattern RR (GE) = RR (G) + RR (E) − 1 RR (GE) > RR (G) + RR (E) − 1

Risks can also be measured on a multiplicative scale where the effect of the risk is measured as a ratio (relative risk) rather than a risk difference. For example, if r(G) is 0.25 and r(00) is 0.10, then the effect of G is 0.25/0.10 = 2.5, the effect of G can then be expressed as r(G)/r(00), the effect associated with E as r(E)/r(00) and the effect associated with the joint GE exposure as r(GE)/r(00). Using this scale the expected patterns of risk and relative risk with and without interaction would be:

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

Model of joint action No interaction Synergistic action

Risk pattern r(GE)/r(G) = r(E)/r(00) r(GE)/r(G) > r(E)/r(00)

Relative risk (RR) pattern RR (GE) = RR (G) × RR (E) RR (GE) > RR (G) × RR (E)

4.8 Which scale should we use to measure GxE ? A given data set can be tested to see how well it conforms to an additive or multiplicative model. However, the question of which scale should be adopted has been heavily contested, though the theoretical literature on sufficient cause models seems to be converging on a consensus advocating use of a fixed reference definition based on the additive scale. This argument integrates the idea that two causal factors from different causal pies (mechanisms) will generally have an additive relationship, whereas component causes from the same mechanism will have a relationship which is super-additive [34]. It is therefore possible that our previous emphasis on multiplicative models has meant missing biological relevant interactions [50]. Further support for use of the additive scale when examining interactions, comes from theoretical work regarding the concept of biological parallelism. It is possible that within the group of individuals exposed to both G and E there may be a subgroup of individuals who would contract the disorder if they were exposed to just one of the risk factors G or E, that is the risk factors act in parallel (|G E|) This conceptualisation of potentially competing risk factors does not fit neatly into the sufficient causal framework, however it has been proposed that it could be accommodated by modifying the model allowing one component of a sufficient cause to be non-definite, containing either G alone, E alone, synergistic GxE or parallel |G E|. Considering parallelism potentially allows the extent of interaction to be quantified, by estimating the proportional size if the subgroup with GxE synergism from the group of individuals who are exposed to both G and E [51]. The actual amount of interaction or parallelism cannot be directly measured in individuals exposed to both

G and E. However, it has been demonstrated that the amount of synergism exceeding parallelism equates to the statistical additive interaction [52]. In practise the amount of interaction has been approximated using contingency tables suggested by Darroch [51]. Approximation of synergy (true interaction effect) |synergism| |x1|

|x2| |parallelism|

r(GE) – r(G) r(G) – R

R(GE) – r(E)

r(E) – r(00)

r(GE) – r(00)

Take, for example, the Finish Adoption study [53]. Diagnosis of maternal schizophrenia was used as a proxy marker for G , while E was the level of communication deviance and thought disorder in the adopted into family and the disease outcome was broadly defined schizophrenia spectrum disorder. The risk of schizophrenia spectrum disorder was around 4% in the group of individuals who were exposed to neither exposure and for those exposed to G alone. The r (E) was 34% and the r (GE) was 62%, therefore filling in the risks for Darroch’s table, (x1 and x2 are unmeasured parameters). Approximation of synergy (true interaction effect) in the Finnish Adoption Study |synergism| |x1|

|x2| |parallelism|

0.58 0

0.28

0.30

0.58

It follows that |x2| must lie somewhere between 0 and 0.30. Therefore |synergism| must be between 0.28 and 0.58. That is, between 45% (0.28/0.62) and 94% (0.58/0.62) of the patients with schizophrenia spectrum disorder exposed to both communication deviance in the family (E) and an affected mother (G) seems to be attributable to GxE. It is possible that the optimum choice of measurement scale may depend on the goal of the investigation. Additive models have certainly been shown to be of greater relevance when assessing the public health impact of interactions as interventions at the population level need to be understood in the context of the prevalence of all other causal factors [49], while some purport that the multiplicative scale is apposite for aetiological research. If the environmental risks have very low variance, 61

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that is they are pervasive, multiplicative GxE models would not be helpful even if the biological reality is that the effect of the genotype is contingent on the environmental exposure. For example, genetically moderated susceptibility to malaria in regions where the infection is endemic would not be demonstrated by epidemiological GxE studies on the multiplicative scale [54]. However, in the absence of specific pathophysiological models of the disorder being studied, the scale chosen to measure interactions will at some level be arbitrary [48]. This concern notwithstanding, some researchers have postulated that the multiplicative scale may be more appropriate when certain causative pathways are being investigated, for example a multistage model of disease progression may best be described on the multiplicative scale, as the onset of the disorder will only occur after a number of iterative stages are completed, that is the stages are independent of each other. For example, genetic factors may influence risk for the first stage of the disorder, and first stage only, whereas an environmental factor may influence risk for a second stage, and second stage only, with the disorder only developing after there has been transition from stage 1 to stage 2 [55]. Under this hypothesis the combined effect of G and E will be equal to the product of the individual effects. Therefore if the magnitude of G effect on the disorder is 10 and the effect size of E equals 2, then the effect of their combined exposure will be 20. Inherent in the use of the multiplicative scale is the idea that the causal factors are independent from each other. However, the current definition of the sufficient component cause framework is deliberately abstract and independent of any specific disease model. It considers component causes acting at different times as biologically interacting (that is they are not considered Independent) if both are necessary components of a specific casual mechanism, so the additive scale still fits. It is important to note that the presence or absence of interaction on the additive scale does not indicate any specific causal model. It is recommended when reporting interactions in scientific journals that sufficient information should be provided to allow the interested reader to interpret the interaction on the additive scale if the multiplicative scale has been used, therefore allowing interpretation in a sufficient causal framework [56]. 62

This can be done by presenting the direct effects of the genetic and environmental risk factor and their joint effect, relative to the group of individuals exposed to neither factor [57]. Another approach is to present the full multiplicative model, including the direct effects and product term so allowing the recalculation of the joint effect on the additive scale [58].

4.9 Study designs for the detection of GxE There are several different study designs that potentially allow GxE to be detected, each with its own strengths and potential problems [59, 60].

4.9.1 Cohort design The cohort study has been the design of choice for common disorders; however rarer disorders and those with late or very wide ranges of age of onset may require sample sizes which are too large to be practically viable. In this design DNA samples and environmental exposure information can be obtained from an initially healthy sample, that is followed up prospectively. As the assessment of the environmental exposure occurs prior to onset of the disorder it is relatively free of information (recall) bias. High rates of follow up are however necessary to reduce selection bias, this can be difficult if the disorder has a long incubation period requiring years or even decades of observation. It is also necessary to try and ensure DNA samples come from a high proportion of both cases and controls, as differential take up can lead to selection bias. Information about ethnic background or genomic control methods [61] should be considered if population stratification is a potential problem due to migration. A nested case–control approach can be used to compare cases with those individuals who did not develop the disorder, and analysed using the group of individuals who have neither exposure to the environmental risk factor or the high risk gene variant as the reference group, so estimating odds ratios. Measured confounding variables can be adjusted for by stratification procedures or by using multivariable modelling such as logistic regression, Poisson regression or Cox’s proportional hazard models [62, 63].

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

4.9.2 Case–control design Generally, case–control studies are more economical than cohort studies. Further, they are potentially powerful methods for the investigation of rarer disorders. Selection bias, particularly due to the selection of controls who may not be representative of the population at risk, is a major limitation. Further, if cases are collected from a clinical setting then the sample is enriched with individuals who are help-seeking. This is especially problematic when investigating less severe disorders as many people will not bother engaging with services for mild disability. Information on environmental exposure is often collected retrospectively, which may result in information (recall) bias, therefore it is preferable if the estimation of previous exposure comes from multiple sources or contemporaneous records. A high and non-differential take up rate for DNA analyses is required if we wish unbiased estimates of genetic main effects and interactions; however, biased main effect estimates for the environmental factor [64] and biased genetic main effects [65] may result in relatively unbiased interaction parameters. If there is an ethnic differential between cases and controls then population stratification could result in spurious gene variant associations. The controls can be unrelated individuals or relatives of the cases. The use of unrelated controls can be analysed by using the group of individuals who have neither exposure to the environmental risk factor or the high-risk gene variant as the reference comparison and estimating odds ratios, controlling for measured confounding variables by stratification procedures. Multivariable methods such as logistic regression, recent traditionally measured interaction terms on the multiplicative scale, but more recently extensions have been developed to assess interactions on the additive scale [66, 67]. When relatives are used as controls, detection of interactions may be more efficient as we are enriching the sample with the high risk gene, However, if the risk variant has a high frequency in the family controls there will be a loss of contrast, which will reduce the study power, such that in the most extreme case, monozygotic twins, testing for GxE will more likely reflect main effects rather than the interaction effect. Each case is matched to one or more unaffected

relative and conditional logistic regression models are used to estimate the GxE. The main threat to the validity of findings from such studies is the problem that both genes and environment are generally shared by family members so correlation on unmatched risk factors within the matched case control pair is likely. Furthermore, gene–environment correlation is built into the design reducing its power to detect GxE. Twin studies share the same disadvantages [68, 69]. Few candidate/susceptibility genes have been replicated in psychiatric disorders to date. When there is no candidate gene known GxE can be measured indirectly using family-based approaches: (i) Case–control studies using both relatives and unrelated (population based) controls. The analytical strategy is to compare the odds ratio for the effect of the environmental factor, in the cases with relative controls, to the odds ratio estimated from the case and non-related controls. The premise is that if there is GxE operating you would expect to find higher odds ratios when relatives are used as controls as compared to the analyses using population-based controls, while you would expect equivalence of the risk across control groups if there was no GxE interaction [59]. Of course it is quite possible that the ‘family effect’ could result from a shared environmental factor which has been unmeasured. (ii) The use of proxy (surrogate) measures of genetic liability such as family history or confirmed intermediate (endo)phenotypes (heritable biomarker, lying along the causal pathway from gene to disorder, but at a more proximal position to the gene, than the manifest symptoms), is also possible.

4.9.3 Case only design When a genotype is independent of an environmental exposure and the disorder is rare, then within the population GxE can be tested in cases only [70]. In this case–case design, the prevalence of the exposure in the genotype-positive cases is expected to be the same as the prevalence of the exposure in the cases without the high risk genetic variant. Thus, statistically significant departures from equal prevalence are indicative of an interaction between genotype and environmental exposure. However, independence of genotype and environmental exposure is rare and gene–environment correlation is generally the rule 63

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rather than the exception. Violation of this assumption of independence has been shown to produce grossly inflated type 1 errors [71]. Furthermore, this method only allows an estimation of interaction not the main effect of the genotype and environment. Simulation studies demonstrate that GxE can be subsumed into main effect of the genotype; therefore this design fails to provide a comprehensive test of the causal mechanism and should only be used with great caution.

however multi-level analytical models are currently being developed to deal with these factors [75]. Multi-generational pedigrees may be useful in order to indirectly test the hypothesis that there has been a change in the penetrance of a known high risk variant over time due to changes in environmental factors, however this approach is most useful when the high risk gene variant is highly penetrant, which is required to allow familiar aggregation to be adequately detected.

4.9.4 Family designs

4.9.5 Gene–environment wide interaction studies (GEWIS)

Sib-pair analyses are linkage techniques based on the simple premise that pairs of phenotypically concordant siblings (the affected sib-pair design) will demonstrate excess sharing of commonly inherited genomic segments, while phenotypically discordant siblings (the unaffected sib pair design) , will tend to have lower proportions of shared variants. By estimating the degree of inter-pair genetic similarity (at the region of interest, or across the genome) should help us identify the chromosomal location of candidate genes. This is achieved by estimating the sharing pattern, that is the number of alleles at a given locus that are the same (identical by descent, IBD). The expected sharing pattern in siblings approximates to z0 = 25% for no identical allele – z1 = 50% for one identical allele and z2 = 25% for two identical alleles. Departure from this pattern suggests linkage and statistical significance can be estimated within the likelihood framework [72, 73]. Sib-pair studies can be extended to include GxE by using stratification or extensions of common multivariable models [74]. Case parent trio design has been used to test candidate gene associations including testing GxE interactions. This model uses the genotypes on all three members of the trio but only the environmental exposure from the case (i.e., a partial case control design). The basic premise of the design is to stratify the genetic relative risk estimates from the caseparent trio, by environmental exposure status of the case. If there is no GxE interaction the two genetic relative risks would be expected to be the same, however if an interaction is present their ratio will be an estimation of the interactive relative risk. Currently stratified analyses are used to control for known within family variables which may influence the risk, 64

The candidate (susceptibility) gene approach to the identification of genetic determinants of common psychiatric disorders is impeded by: • Lack of a definitive allelic architecture model for the disorders: the polygenetic model is generally considered the best approximation; however, this has been strongly contested [76]. • Substantial gaps in pathophysiological understanding of the disorders. If the multifactorial (polygenetic) model is a good approximation to the allelic architecture of common psychiatric disorders, GWAS will provide a potentially unbiased method to search the genome for causative variants of small effect [77]. However, we should bear in mind that if substantial allelic heterogeneity is present, due to rare variants or epigenetic phenomena (i.e., low allelic identity) this method will be less successful as each genetic variant will arise from an independent haplotype (set of genetic markers in DL) background, so cancelling out each other’s signal [78, 79]. Experience from GWAS in non-psychiatric conditions suggests that for some disorders as many as 30 000 cases and similar numbers of controls will be required to robustly identify highrisk genetic variants [77]. Such large-scale studies have led to the formation of consortia to coordinate the development of such methodology and carry out the studies in psychiatry [80]. To date, GWAS methods have only been used to detect main (direct) effects of single or linked (haplotypes) markers. GWAS SNPs cover more than 4/5th of the SNPs known to HapMap (http://www

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

.hapmap.org) CNVs are also detected but with less reliability using current technology. However, in complex multi-factorial diseases, scanning for main effects might miss important genetic variants, especially in subgroups of individuals with specific environmental exposure interactions. Furthermore, GxE with opposite effects in groups with different exposure profiles, that is crossing interaction will not be identified, as no direct main effect will be found. Therefore, to be clinically relevant GWAS will have to be placed in an epidemiological and public health context. One way of doing this is to enrich GWAS with environmental information – a technique known as GEWIS. No GEWIS study has yet been done, due to considerable methodological and logistic challenges, however a number of analytical approaches have been proposed which attempt to deal with the substantial problems of prior probability errors which will occur when estimating main effects on 1 000 000 or more markers, which is even more likely with concomitant estimation of E exposures and GxE. GEWIS studies will therefore require new statistical approaches as the current log linear regression methods do not effectively test the global null hypothesis of a genetic variant not being associated with the disorder in any of E strata. Extensions of the interaction methods beyond the currently employed simple departures from additive (or multiplicative) joint effects will be required, most likely based on multivariate latent variable modelling techniques that can deal with ‘mega-variate’ data [81–83].

4.10 Threats to the validity of epidemiological GxE studies The study designs discussed in this chapter are (observational) epidemiological in nature, therefore the genotype, environmental risk exposure and the pathology are studied as they occur within the population and as such their findings need to be interpreted, in the light of potential bias (systematic errors) and confounding (mixing the effect of extraneous variables with the effects of the exposures under study). Such issues can be reviewed in any comprehensive textbook of epidemiology [84]. There are however specific threats to the validity of

GxE epidemiological studies including unmeasured GEr, population stratification effects and sample size and power issues, which we will discuss here.

4.10.1 Confounding by gene–environment correlation GxE analyses are based on the assumption that the environmental and genetic exposures are independent. However, it is clear a number of the exposures we conceptualise as ‘environmental’ have a significant genetic contribution, for example stressful life events and substance use both have demonstrable gene–family-environment covariance [85]. Case only , partial case–control and family methods are sensitive to even statistically non-significant GEr, while case–control and cohort designs are slightly more robust [86, 87]. A number of strategies can be used, preferably in combination to reduce GEr confounding. 1 Careful selection and measurement of environmental exposures. The retrospective measurement of environmental exposures using self report questionnaires are prone to recall bias, as variation in recall is likely to be behaviourally mediated by an individual’s personality, potentially leading to non causal GEr. Therefore in case–control studies that rely on retrospective measures, multiple informant sources and contemporaneous records should be sought. 2 Careful selection and measurement of proxy (surrogate) measures of genetic risk. Proxy measures of genetic liability such as family history or intermediate phenotypes can be used in omnibus (assumes a single unified interaction between the unidentified genes) models for GxE, with care. These are clearly related to genetic liability. However, while dimensions of personality and life events, such as adversity, are in part genetically determined, it would be invalid to substitute such surrogates as genetic risk markers as they are influenced by both genetic and environmental factors. 3 Stratification analyses are undertaken to determine whether the relationship between environmental exposures is modified by the genotype variants. That is, stratification by genotype subgroup. 65

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This can also be performed using genotype-specific disease – exposure odds ratios; interstrata differences are compared using likelihood ratio tests of homogeneity. Theoretically GEr can be controlled for by enforcing independence of G and E in loglinear models; however, such tests generally have low power to detect meaningful departures from independence [88]. 4 Compare prevalence of exposure in relatives as compared to non-related controls. These analyses are based on the premise that rates will be higher in relative controls as compared to population controls if there is a genetic effect uncontrolled for shared environmental influences, suggesting GEr. However, if there is no difference in exposure prevalence across the two control groups, GEr is less likely. Of course the most effective way to control for GEr in GxE studies is to use an experimental paradigm. While it would be unethical to allocate individuals to adverse environmental exposures, it may be possible to develop ‘harmless’ analogues of environmental adversity. An elegant example of this approach used standard emotional stimuli as a surrogate for vulnerability to stress in an functional magnetic resonance imaging study [89]. GxE strategies have been shown to be effective in the assessment of pharmacological interventions (pharmacogenetics) [90].

4.10.2 Population stratification When unrelated controls are used in case–control and cohort-designed GxE, the studies are potentially susceptible to confounding by ethnicity (migration), which in the genetic literature is termed population stratification confounding. Population stratification describes the gradients observed in gene frequencies, within broad ethnic groupings, that is there are potentially unmeasured genetic subpopulations. If these subgroups are unequally distributed between cases and controls, biased estimates of effect could be possible if subpopulation genetic variations are correlated with unmeasured environmental risk factor. Potentially more problematic, is the possibility of statistical over-dispersion (i.e., greater variability observed in the data than would be expected based on a given simple statistical model) 66

when subpopulations are present. Simulation studies suggest that even small amounts of stratification have significant consequences in large samples [91], though some commentators have refuted this claim [92]. While family-based designs overcome the potential of confounding by population stratification, they are subject to other problems as discussed above. Population stratification can, however, be effectively handled using genomic control approaches [61, 93].

4.10.3 Power, sample size and issues of multiple comparisons Power and sample size calculations are critical in the design of GxE studies and will vary according to the design used. However, it should be stressed that sample size is only one factor in determining power. The statistical power of any GxE study will also depend on the strength of the interaction effect, the variability of the environmental exposure, the frequency of the genetic variant in the population and the accuracy (reliability and validity) of the measured gene, environment and disorder (or pathological outcome) [94]. Uher [32] has demonstrated the impact of these factors in simulation studies. Strong effects were evident in the presence of variation in the reliability of environmental and pathological measures. A decrease of just 0.2 in both measures equated to losing half of the sample size [32]. Therefore, smaller studies with high quality accurate discriminative measures of environmental and pathological outcomes may be advantageous in many circumstances [95]. Simulation studies clearly show how the frequency and variability of the environmental exposures influence study power. One potential approach to handling exposure variation effects is to sample subjects from both extremes of the exposure distribution (very low and very high doses). Simulation studies suggest this effectively increases the power for detecting GxE, especially when the exposure is measured on a quantitative scale, though this approach requires further simulation testing [96]. Sample size calculations estimate the minimum number of subjects necessary to provide sufficient power to detect a GxE, if it is truly present. GxE as a higher order effect, require larger sample sizes as compared to designs which only measure main

EXAMINING GENE–ENVIRONMENT INTERPLAY IN PSYCHIATRIC DISORDERS

effects. A number of different statistical methods have been described that estimate the sample size requirements to detect GxE [97–99]. How to handle multiple comparisons is a major problem facing genetic epidemiology generally and GxE investigators in particular. The problem of potential type 1 errors (false positives) has traditionally been handled by making corrections for multiple testing, based on the probability of making at least 1 spurious positive inference; however such techniques are conservative as they do not take account of linkage between multiple genetic markers. This has lead to the development of rates based on the false discovery rate (FDR). Many such rates have recently been published and preserve greater power to detect true positive interactions. There is no consensus on how best to handle issues of multiple testing, with other techniques based on permutation methods and sequential multiple-decision procedures currently being developed [35]. While false positive findings in GxE will occur, perhaps a much commoner problem is actually type 2 errors, that is accepting the null hypothesis as a result of inherent low power in our statistical models [99, 100].

4.11 Epigenetic mechanisms As well as genes influencing the exposure and susceptibility to environmental exposures, through GEr and GxE, the reverse association is also possible, and has been postulated in a number of psychiatric disorders, including depression, schizophrenia, substance dependence and developmental disorders. Epigenetic mechanisms occur when environmental factors impact on DNA sequencing (causing de novo mutations) or through changes in DNA methylation and chromatin structure (causing altered gene expression through epimutations) both globally and at the promoters of candidate gene sites. For example, epigenetic chromatin remodelling of the brain derived neurotrophic factor promoter site (BDNF) is associated with neuronal activity, seizures, chronic stress, cocaine addiction and Rett’s syndrome: remodelling at the reelin promoter may play a role in mouse models of schizophrenia [101]. Although research on DNA methylation as an epigenetic mechanism underlying GxE is only in its early

stages the preliminary results are promising. Animal studies have shown early maternal behaviour predict the offspring’s stress sensitivity through altered DNA methylation in some key neuronal receptor genes that are involved in the stress response [102]. Environmentally induced epigenetic mechanisms may explain a range of epidemiological findings including the age of onset curves, monozygote discordance and the gender differences observed in psychiatric disorders. Methodologies designed to investigate such epigenetic processes are being developed currently and are likely to further elucidate the gene–environment interplay in psychiatric disorders [103].

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5

Reliability Patrick E. Shrout Department of Psychology, New York University, NY, USA

5.1 Introduction In psychiatric epidemiology, assessment of mental conditions and of risks for psychiatric disorder relies heavily on information provided by patients (or survey respondents) and by informants who are close to the patient/respondent. How good is the information provided by these people, and how good are the assessment inferences that we make on the basis of this information? The quality of the assessment in psychiatry and epidemiology is typically characterised by the reliability and validity of the measure. Reliability is the degree to which a measurement is reproducible and not affected by transient assessment noise. Validity is the degree to which the measurement is useful. Although validity is the ultimate criterion by which to judge a measure, we know that a measure will not be useful if it is dominated by measurement noise. This means that reliability is a necessary condition for validity, but it is not sufficient to guarantee validity. Even though reliability is only an intermediate step towards quality measurement, it is often methodologically interesting because it is a problem that can usually be fixed. Reliability can be improved by structuring and standardising the assessment procedure, by improving the training of both the respondents and those carrying out the assessment and by averaging replicate measurements. If problems of unreliability are not addressed, then subsequent problems of validity are intractable. This is why reliability was given so much attention in developing the Versions III and IV of the Diagnostic and Statistical Manual of the American Psychiatric Association [1, 2].

Epidemiologists must attend both to the reliability of diagnostic measures and risk measures. Two features of psychiatric epidemiology make reliability more of an enduring problem in this field than in others. One feature is the previously mentioned dependence on information provided by respondents or informants. Respondent reports present many opportunities for noise to enter the recorded data: the understanding of the question, the recall and reporting of the answer and the coding and entry of the data. The other feature is the epidemiologists’ search for novel populations and risk groups that might provide clues to the aetiology of mental disorders. New populations require new assessments of reliability, since populations vary in language, literacy and cultural expression of disorders. As we will see, the variability of the trait under study in the new population also affects the reliability of measures.

5.2 The reliability coefficient Consider a single measurement procedure. Respondents are sampled from a specific population, measured in some way and assigned a numerical value, that is represented by the variable X. If the characteristic being measured is qualitative, such as having a certain diagnosis, then the variable X might be defined to be binary, that is X = 1 if the respondent has the characteristic, and X = 0 otherwise. If the characteristic is quantitative, such as severity of illness or exposure, then X might be defined to take some well-specified numerical score. 2 The variance of X, σX , is a population parameter that describes how much the measurements differ from person to person in the population being

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

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CHAPTER 5 2 studied. In some populations σX might be relatively small, while in other populations the variance might be large. Small variance implies that the measurement distinction is subtle in the population, while large variation implies the opposite. In populations with small overall variation in X, any measurement error may be quite serious. According to classic reliability theory, it is useful to 2 2 decompose σX into two components, σX = σE2 + σT2 , 2 where σE is variance due to measurement noise and σT2 is variance due to systematic differences between persons being measured. We will discuss how these two components are estimated later. This decomposition implies that random measurement noise increases the total measurement variation. If measurement errors can be eliminated, then the error variance, σE2 , goes to zero and the total variance shrinks to σT2 . If errors dominate the measurement, 2 then the majority of σX may be attributable to σE2 , even if there is systematic variation between persons, that is of interest. In its purest form, the reliability coefficient, RX , is 2 a ratio of the population parameters, σT2 and σX :

RX =

σT2 2 σX

=

σT2 [σT2

+ σE2 ]

(5.1)

RX varies from zero (X is due entirely to unsystematic stochastic processes) to unity (X is due entirely to systematic individual differences). It can be thought 2 of as the proportion of σX that represents genuine, replicable differences in subjects. It turns out to be a useful quantity in statistical analyses as well. For example, it can be shown that the correlation between X and another variable Y will get smaller as the reliability coefficient of either variable gets smaller [3, 4]. Knowledge of reliability can also be used to adjust for bias [5] and to obtain more powerful tests of group differences [6]. How do we evaluate different values of RX ? If we know that a measure truly has a reliability of 0.50, then we know that only half its variance is systematic. That may not be what we hope for, but it might be good enough for some preliminary studies. For more definitive studies, we should aim to have reliability above 0.80. To provide some interpretive guidelines, Shrout [7] recommends the following characterisations of reliability values: (0.00,0.10), virtually no reliability; (0.11,0.40), slight; (0.41,0.60), fair; 74

(0.61,0.80), moderate; (0.81,1.0), substantial reliability.1 For a complete development of RX and its implications, see Lord and Novick [8] or Dunn [9].

5.3 Designs for estimating reliability To estimate RX we need to define what is meant by systematic variation of X. Classical psychometric theory defines this hypothetically. Suppose that a subject is selected and is measured once to produce the score X1 . Now suppose that it is possible to make the measurement over and over again without affecting the subject, and without recall of the previous Xj values (where j indexes each replicate measure). Classical measurement theory defines the systematic part of X to be the average of all of these hypothetically infinite measurements of the selected subject. This systematic component of the measurement is written as T = E(X), which is interpreted as the expected average of the many replications of X. Note that if the measurement were height or weight, then it would actually be possible to take many repeated measurements of this sort. In psychiatric epidemiology, reliability is estimated by approaching the hypothetical ideal with approximately replicate measurements. If there is virtually no variation across replications of X, then we infer that σE2 is small in magnitude, and that reliability is very good. If variation across replications is observed, then the magnitude of the within-subject variation is compared to that of the between subject variation using the definition of RX in Equation 5.1 above. The most common replication design calls for making the X measurement at two points in time (the test–retest design). Variation in the X values across replications and across respondents is used to 2 estimate σE2 , σT2 and σX , and these can be used to estimate RX . The formal equations for these estimates are presented in a later section. Although theoretically and intuitively appealing, the test-retest design falls short of the hypothetical ideal in several ways. On one hand, the second measurement is often affected by systematic 1 In setting standards for reliability, however, we must be aware that estimates of reliability may be smaller than the actual reliability because of systematic bias, which is discussed later.

RELIABILITY

biological, psychological and social changes in the respondent. These systematic changes make the estimate of σE2 appear larger than it would have been at a single measurement instance. When legitimate change is included with error, the estimate of the reliability of the first assessment is too small. On the other hand, if the respondents remember their original responses, and then try to be ‘good’ by reporting the same thing, then the reliability estimate may be too large. Methodologists who address these opposing biases recommend that the second assessments be carried out after a long enough period to reduce memory artefacts, but promptly enough to reduce the probability of systematic changes. Recommendations of how long the period should be are more products of opinion than science, but 2 weeks often seems to work well. Test–retest designs can be used with the whole range of measures made in psychiatric epidemiology. Interviews, questionnaires, ratings and physical measurements can all be repeated after an appropriate time. It is not always necessary, however, to wait to obtain a replicate measurement. When the measurement is a judgement, such as the Global Assessment Scale [10], it is possible to have two independent ratings made at the same time. Moreover, time can be frozen by video-recording the structured interview so that ratings can be obtained from those viewing the recording. Although these alternatives to traditional test–retest designs overcome the confounding of unreliability with genuine growth or development, they bring with them their own problems. These have been discussed by several authors, including [11]. Insofar as the respondent’s idiosyncratic responses contribute to unreliability, then estimates based on a single recorded interview may underestimate the level of random variation in the actual ratings obtained in the field. For this reason, inter-rater reliability studies using recorded interviews are expected to overestimate true reliability. When the measurement procedure under study is a questionnaire that includes several items pertaining to a single underlying psychological trait or symptom dimension, it is also possible to obtain some information about reliability within a single assessment occasion. The items that relate to the same underlying concept are considered to be replications of each other. The degree to which the patterns of

responses suggest that they are empirically related is used as evidence of reliability. This inference is made on the basis of the internal consistency of the questionnaire responses. The most widely used measure of reliability based on internal consistency is coefficient alpha [12]. An alternate measure is McDonald’s omega [13]. Internal consistency measures of reliability are affected by some biases that make them underestimate actual reliability [14], and others that make them overestimate reliability [15]. They will underestimate reliability if the items within the set are not close replications of each other. For example, a scale of depression symptoms may contain some items on mood, others on psychophysiological complaints and yet others on cognitive beliefs. Although these are all expected to be related to depression, they are not exact replications of each other. To the degree that the correlations among the items is due to the different item content rather than error, the overall reliability estimate will be smaller than it should be. Reliability may be overestimated by the internal consistency design if the whole interview is affected by irrelevant global response patterns, such as mood or response biases. For instance, some respondents may perceive that acknowledging symptoms is socially undesirable, and may systematically under report more bizarre problems. Others may fall into a pattern of denying everything. These so-called response biases inflate internal consistency reliability estimates. They are often addressed by mixing the items across many conceptual domains, editing the items so that half are keyed as a symptom when the respondent says ‘no’ and half are keyed the opposite way. Scales of Yea-saying, and Need-forapproval are also sometimes constructed to identify those respondents who are susceptible to response biases. The validity of these scales, however, is a subject of open discussion. Given the possibility of opposing biases, how should we evaluate internal consistency results? If the results appear to indicate high reliability, look for response artifacts that might have inflated the estimate. If provisions have been taken to address response biases, then the high level of reliability might be real. If the results indicate that there is low reliability, then look to see if the items included within the internal consistency analysis are heterogeneous 75

CHAPTER 5

in content. It is possible that a set of items that are heterogeneous might have adequate test–retest reliability even though the internal consistency estimate is low. Because researchers often seem unaware of the ambiguity of reliability results based on calculations of Cronbach’s alpha from one administration of a measure, a number of psychometric experts have recommended that reliability be measured other ways (e.g. [14, 16]). It is always helpful to incorporate multiple designs into a reliability program. By systematically studying the kinds of replication, one can gain an insight into sources of measurement variation. This is what is recommended by Cronbach and his colleagues [17] in their comprehensive extension of classical test theory known as Generalisability Theory. This theory encompasses both reliability and validity by asking about the extent to which a measurement procedure works in different populations, at different times, with different raters, who may have different training. This broad perspective easily included designs such as those on the Diagnostic Interview Schedule (DIS) [18] that compared results from interviews done by ‘lay’ interviewers to those done by mental health professionals. To the extent that the trained lay interviewers performed like the professionals, the results might be interpreted as test–retest reliability of the DIS. If the level of training actually made a difference, then the results might be interpreted as the validity of using lay interviewers (assuming that the professionals are the ideal interviewers for this structured measure). From the generalisability perspective, it is neither a reliability or validity study, but rather a study of the generalisability of DIS results across time and interviewer-type (see [19]). The flexibility of Generalisability Theory was illustrated by Cranford et al. [20], who used this approach be used to estimate reliability of changes in affect over days in a diary study. These reliability procedures have great utility for epidemiological studies of the course and temporal correlates of pathology.

5.3.1 The effect of population variance on reliability In all of the reliability designs reviewed above we assumed that respondents were sampled from the population, that is to be studied. By randomly sampling 76

from the population, we can obtain an unbiased esti2 mate of σX . Note that any bias, that is introduced in 2 estimating σX can have serious effects on the estimate of RX . Epidemiologists should be especially sensitive to the fact that samples of patients should not be used in a reliability study if the ultimate survey is to be carried out in the general population. Relative to the variance in community surveys, the variance of most psychiatric measures will be too large in treated samples. The bias is usually concentrated in the σT2 term 2 of σX = σT2 + σE2 and thus the reliability often appears to be better in the treated population than in a community population. When the reliability study sample has been constructed using stratified samples of cases and non-cases, then it is often possible to undo the bias through weighting (e.g. [21]).

5.4 Statistical remedies for low reliability If an investigator discovers that a quantitative measure is not sufficiently reproducible, there are several remedies that have been mentioned briefly before. The measure itself can be changed, the training of those administering it can be improved, or perhaps some special instructions can be developed for the respondents that improve the purity of the measurement outcome. These are examples of procedural remedies that are often effective. There is also a statistical remedy: Obtain several independent replicate measurements and average their results. The idea is simple: averages of replicate measures are by definition more systematic than the individual measures themselves, so the reliability of the sum or average of items or ratings will be consistently higher than that of the components. The degree to which reliability is expected to improve in the composites is described mathematically by Spearman [22] and Brown [23]. Let the sum of k ratings or items (X1 , X2 , X3 , . . ., Xk ) be called W(k). Then the expected reliability of W(k) can be written as a function of k and the reliability of the typical measurement, RX , according to the Spearman–Brown formula: RW(k) =

kRX . 1 + (k − 1)RX

(5.2)

Equation 5.2 is based on assumptions about the comparability of the measurements that are averaged

RELIABILITY

or summed into W(k), not on the form or distribution of the individual measurements. Because the result is not limited by the distribution of the X measures, the formula is even useful in calculating the expected reliability of a scale composed of k binary (0,1) items as well as scales composed of quantitative ratings or items. Note that averaging measures only is a remedy for low reliability if there is some evidence of replicability. It is clear that RW will be zero if RX is zero, regardless of the magnitude of k. The Spearman–Brown formula is especially useful for internal consistency reliability studies. When multiple items are available as replicate measures, it is usually the reliability of the scale score (the sum or average of items) that is of interest. While we could use the internal consistency design to calculate the average item reliability, and then use that result in Equation 5.2 to calculate the expected scale reliability, these steps are combined when one uses certain estimation formulas, such as the classic coefficient alpha of Cronbach [12]. The relationship described in the Spearman–Brown formula can also be used in studies of interrater reliability to determine how many independent ratings need to be averaged to obtain an ideal level of reliability, say CR . If the obtained level of reliability for a single rater is RX , then the number of raters that are needed to produce an averaged-rater reliability of CR is k=

CR (1 − RX ) . RX (1 − CR )

(5.3)

For example, if each rater only has a reliability of RX = 0.40 and one wants a reliability of CR = 0.75, then Equation 5.3 gives k = 4.5. This means that averages of four raters would be expected to have less than 0.75 reliability, while averages of five raters would exceed the target reliability of 0.75.

5.5 Reliability theory and binary judgements The reliability theory just reviewed does not make strong assumptions about the kind of measurement embodied in X, and indeed many of the results hold for binary variables such as ones that might represent specific psychiatric diagnoses (e.g. X = 1 when the respondent is thought to have current

major depression, X = 0 otherwise). Kraemer [24] has shown explicitly how the results work with binary judgements. From her mathematical analysis of the problem it can be seen that the systematic component of X that I have called T = E(X), will end up as a proportion falling between the extremes of 0 and 1. It represents the expected proportion of diagnosticians who would give the diagnosis to the respondent being evaluated. If T is close to 1, then most diagnosticians would say that the respondent is a case, and if T is close to 0, then most would say that the respondent is not a case. Note that while X itself is binary, T is quantitative in the range (0,1). Because averages are quantitative (at least as n gets large), the psychometric results from the Spearman–Brown formula are applicable only when the composite of interest is quantitative. This is often the case when X represents binary items in a symptom scale. Of interest is the count of symptoms, which is closely related to the average of symptom items. However, if we really want a binary variable as the outcome, then the Spearman–Brown result does not apply. For example, diagnoses of several independent judges are sometimes combined into a ‘consensus diagnosis’, that is itself binary. If the consensus rule is one that requires that all judges make the diagnosis before the diagnosis is applied, the result might be less reliable than some of the individual diagnosticians (see [25]). The total consensus rule is as weak as the least reliable diagnostician, because each has veto power regarding whether the consensual diagnosis is made. Many of the classic psychometric results depend on the assumed symmetry of errors. Because T is defined as an average, by definition about half the errors go in one direction and half in the other. For diagnoses, however, the errors that attract attention are those that seem to cause clinically relevant discrepancies. For example, if we know that a certain set of presentation facts are viewed by 90% of trained clinicians as indicating schizophrenia, then the clinically relevant discrepancies are those diagnosticians who argue that the diagnosis of schizophrenia is inappropriate. Persons who insist that schizophrenia should be diagnosed with more than 90% certainty are not usually considered in practical terms to be outliers. The interest in the asymmetry of errors in diagnoses prompts some researchers to decompose 77

CHAPTER 5

interrater discrepancies into ones that are consistent with problems of sensitivity and specificity. From this perspective it can be shown that the reliability coefficient of Equation 5.1 is a function of both kinds of errors. If we focus on one kind of error only, such as sensitivity, the classic relation between reliability and validity no longer holds necessarily. There are some examples in which different levels of reliability are consistent with the same level of sensitivity. (One usually finds that the assumed specificity or prevalence varies with the reliability in examples such as this.; see [26].) When asymmetric errors are of central interest, the results reviewed in this chapter may not be totally applicable. The role of asymmetric errors in binary ratings is only one special aspect of such data. Another is the relation of the expected mean of a binary variable and the expected variance of that variable. For variables that are normally distributed the mean contains no information about the variance of the variable, but for variables that are binomial (a very common distribution for binary variables), the variance is necessarily small for variables with means near 0 or 1. This fact has implications in the interpretation of Equation (5.1), the definition of the reliability coefficient. If the prevalence of a diagnosis is low in a population, then σT2 will be small. If the level of error variance is held constant, but σT2 is made smaller, then RX will be smaller. One way to interpret this result is that the level of error must be reduced to study disorders that have smaller base rates in the population. Any randomly false positive diagnosis makes the diagnostic system seem unreliable for rare disorders. In this case the diagnostic system is unreliable because the precious few true positives are swamped by the random false positives. Nevertheless, the fact that reliability is empirically related to prevalence has caused some commentators to question the utility of reliability measures in binary variables [27–29]. Others of us have argued that dropping the statistic because of the challenge of measuring rare disorders is misguided [7, 30] because the reliability statistic is useful in describing the effects of measurement error on statistical analyses. Kraemer [31] lucidly reviewed the rationale of reliability studies and showed how the challenge of establishing reliability of categorical data is affected by various features of the measurement situation and the design of the reliability study. 78

In the next section I present a survey of reliability statistics that can be used to evaluate data from reliability studies. One of these statistics is Cohen’s kappa [32]. It is especially designed for categorical outcomes, but it shares with the quantitative statistics its interpretation as estimators of the reliability coefficient in Equation 5.1 Although the special features of binary data require a careful consideration of the effects of errors in epidemiological analyses, the general concerns for the concept of reliability as reviewed in the preceding sections are usually relevant for multivariate analyses that treat binary distinctions as dummy variables.

5.6 Reliability statistics: General As we have seen, the reliability coefficient of Equation 5.1 is defined in terms of variances: variances of systematic person characteristics σT2 , and variances of measurements across replications for a single person, σE2 . There are several ways to estimate the variance ratio shown in Equation 5.1 [9], but one direct method is simply to estimate the separate variance components and then combine them in the form of Equation 5.1 Estimates of this sort are called intraclass correlations. Intraclass correlation is not a single statistic, but rather a family of statistics that can be used for estimating reliability. In this section we will review several versions that can be used with a wide variety of variables. We focus here on the easiest part of reliability analysis, ‘point estimation’ of the statistic that summarises the reliability results. Although it is important, we do not have the space to present the methods that must be used to estimate 95% confidence intervals for the study results. The form of the interval estimators depends on the nature and distribution of the data, and new methods are being actively developed in the literature. For reviews of methods for confidence intervals see Shrout [7], Dunn [9] and Blackman and Koval [33]. It is important to note, however, that estimates of reliability are often less precise than we would like [34], and that this fact is made clear by the use of confidence intervals. The intraclass correlation point estimates are derived from information summarised in the analysis of variance (ANOVA) of the data from the reliability

RELIABILITY

study. The ANOVA treats each subject as a level of the SUBJECTS factor. Usually subjects are considered to be a random factor, because they are selected to be representative of a population of interest. If the replicate measurements of the subjects are systematically obtained using a certain set of k raters or measuring devices, then the ANOVA might involve a two-way SUBJECTS by MEASURES design. If, on the other hand, the replicate measurements of each subject are obtained by randomly sampling k measures, then the analysis would use a one-way ANOVA.

Table 5.1 Hypothetical data on functioning of 10 probands by three of their relatives.

5.6.1 One-way ANOVA analyses

subjects’ mean ratings are larger than the disagreements among relatives regarding the subjects’ scores. The reliability estimate for the one-way ANOVA is calculated using the first formula in Table 5.3A. This form of the intraclass correlation was called ICR (1,1) by Shrout and Fleiss [36], and we retain that designation. To illustrate the calculation with the numerical example from Table 5.1, we find,

Table 5.1 illustrates data that might be collected in reliability study of relative informants. Each of N = 10 probands is rated by k = 3 distinct relatives. Between-subject variation can be estimated using all k ratings, and within-subject variation is used to estimate the magnitude of the error variation. When the relationships of the relatives vary from proband to probands (e.g. siblings for one proband, parents for another, cousins for a third), these data do not have a data analytic structure for informant. If there had been such a structure, we might have considered a proband-by-relationship two-way ANOVA. In our analysis we will assume that the informants are essentially a random sample of possible informants for a given respondent. Table 5.2 shows the layout of the one-way ANOVA, along with the numerical estimates obtained from the data in Table 5.1. The actual computation of the ANOVA results can be obtained from standard computer software, such as SPSS RELIABILITY [35]. The numerical example illustrates a pattern in which the between-subjects (probands) mean squares is substantially larger than the withinsubjects mean squares. Consistent with an informal examination of the hypothetical data in Table 5.1, this pattern suggests that the differences between

Proband

Relative 1

Relative 2

Relative 3

29 23 19 6 13 0 10 5 31 15

32 33 17 10 20 0 11 1 26 17

17 28 18 5 20 2 15 15 19 18

1 2 3 4 5 6 7 8 9 10

ICR(1, 1) = (251.0 − 22.2)/(251.0 + 2 ∗ 22.2) = 0.77 This result describes the reliability of a single randomly selected informant. About 77% of the variance of a single informant’s ratings is attributable to systematic differences between subjects. Although the stability of the result might be questioned because of the limited sample size, the result is encouraging that this rating, in this population appears to be made fairly reliably by a single informant. Suppose that it is possible to obtain three informant ratings for each subject in the survey. How much more reliable would the average of the three ratings be than an individual informant? The answer can be calculated using the Spearman–Brown formula (Equation 5.2), with k = 3 and RX = 0.77. Alternatively, one can use the formula for ICR(1,k)

Table 5.2 Analysis of variance when replications are nested within subjects: one way ANOVA. Source of variation Between subjects Within subjects

df

Sums of squares

Mean squares

Table 5.1 Example: MS on df

n−1 n(k − 1)

BSS WSS

BMS = BSS/(n − 1) WMS = WSS/[n(k − 1)]

BMS = 251.0 on 9 df WMS = 22.2 on 20 df

79

CHAPTER 5 Table 5.3

Versions of intraclass correlation statistics useful for various reliability designs.

Type of reliability study design

Raters fixed or random? Version of intraclass correlationa

(A) Reliability of single rater Nested: n subjects rated by k different raters

Random

ICR(1,1) =

BMS − WMS . BMS + (k − 1)WMS

Subject by rater crossed design

Random

ICR(2,1) =

TMS − EMS . TMS + (k − 1)EMS + k(JMS − EMS)/n

Subject by rater crossed design

Fixed

ICR(3,1) =

TMS − EMS . TMS + (k − 1)EMS

Nested: n subjects rated by k different raters

Random

ICR(1,k) =

BMS − WMS . BMS

Subject by rater crossed design

Random

Subject by rater crossed design

Fixed

(B) Reliability of the average of k ratings

TMS − EMS . TMS + (JMS − EMS)/n TMS − EMS . ICR(3,k) = TMS ICR(2,k) =

a BMS

and WMS refer to between-subject and within-subject mean squares from a one way ANOVA. TMS, JMS and EMS refer to between-subjects (targets), between measures (judges) and error mean squares from two way ANOVA based on n target-subjects and k raters.

shown in Table 5.3B. This formula is obtained by algebraically combining the expression for ICR(1,1) with the Spearman–Brown formula. In this case the answer is ICR(1,k) = 0.91. About 91% of the variance of the average of three randomly chosen informants is attributable to systematic differences between subjects.

5.6.2 Two-way ANOVA analyses Table 5.4 illustrates data that might be collected in a reliability study of two professional raters or interviewers. As a result of the interview by Interviewer 1 we have both a binary diagnosis (disorder present [X = 1] vs. disorder absent [X = 0]) and a quantitative score such as a total functioning score (called Z in the table). Replicate scores and diagnoses are obtained by a second interviewer, called Interviewer 2. The hypothetical data on X1, X2, Z1 and Z2 are shown for 17 respondents. The layout of the two-way ANOVA is shown in Table 5.5, along with numerical results from the Table 5.4 examples. Only two interviewers were used in the reliability study illustrated in Table 5.4, but we might consider the two to be a random sample from all possible interviewers from the study. If so, then they must not be selected on the basis of their special skills as interviewers, but rather should be selected to be 80

Table 5.4 Hypothetical data on assessment of depression and functioning. X1 and X2 represent test–retest diagnoses of major depression (X = 1, present; X = 0, not present), and Z1 and Z2 represent ratings of adaptive functioning. Respondent 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17

X1

X2

Z1

Z2

0 1 0 0 0 0 0 0 1 0 0 1 0 0 0 0 0

1 1 0 0 0 0 0 0 0 1 0 1 0 0 0 0 0

17 17 26 24 19 22 17 23 19 18 21 13 21 22 15 20 21

11 15 25 22 14 16 18 19 16 12 18 11 23 17 12 18 20

representative. When interviewers who are employed in the reliability study represent the population of potential interviewers, we say that they are random effects. In some cases we are interested in the ratings of specific interviewers rather than a population of

RELIABILITY Table 5.5 Analysis of variance when replications have structure: two way ANOVA. Source of variation

df

Sums of squares

Mean squares

Table 5.4 Examples: Mean square on df

Between subjects (targets)

n−1

TSS

TMS = TSS/(n − 1)

Variable X: 0.254 on 16 df Variable Z: 25.7 on 16 df

Between measures (judges)

(k − 1)

JSS

JMS = JSS/(k − 1)

Variable X: 0.029 on 1 df Variable Z: 67.8 on 1 df

(n − 1)(k − 1)

ESS

Residual (error)

interviewers. Suppose Interviewer 1 is a doctoral candidate who carried out her own data collection, and that Interviewer 2 is a colleague who is hired to document that the ratings are systematic. In this case we simply wish to describe the quality of data collected by the doctoral candidate, and we say that the interviewers are fixed effects. Depending on whether the raters are considered to be random or fixed, we use different versions of the intraclass correlation to estimate reliability. When we wish to estimate the reliability of a randomly sampled interviewer, we use the expression for ICR(2,1) shown in of Table 5.3A. This intraclass correlation is not only a function of the betweensubjects mean squares and the error mean squares, but also the between-measure (judge) mean squares. If different raters are more or less liberal in assigning high scores, then the final variability of the ratings will be affected. ICR(2,1) takes this extra variation into account in estimating reliability. In the two examples of Table 5.4, one reveals a large between-measure effect and the other does not. From the numbers in Table 5.4 it can be seen that the Z2 ratings are usually smaller than the Z1 ratings. Rater 2 seems to believe that most subjects are functioning somewhat worse than perceived by Rater 1. Even with this rater difference, the reliability of Z is higher than the reliability of X, according to the data in Table 5.4. The ICR(2,1) for Z is calculated as (25.7 − 2.67)/(25.7 + (1) ∗ 2.67 + 2 ∗ (67.8 − 2.67)/17) = 0.64 The ICR(2,1) for X is calculated as (0.254 − 0.092)/(0.254 + (1) ∗ 0.092 + 2 ∗ (0.029 − 0.092)/17) = 0.48

EMS =

ESS (n − 1)(k − 1)

Variable X: 0.092 on 16 df Variable Z: 2.67 on 16 df

For the rating of adaptive functioning we could consider averaging both individual Z ratings to obtain a more reliable score. We can use either the Spearman–Brown formula, or the expression ICR(2,k) to calculate the reliability of the mean of two such ratings. In this case, the result is 0.78 rather than 0.64. Although the reliability of the binary X variable is worse than that of the quantitative Z variable, it would not usually be meaningful to rely on an average diagnosis instead of a truly binary rating. For this reason the ICR(2,k) form of the intraclass correlation would not be applied to X in Table 5.4. The calculations carried out so far have assumed that the two sets of ratings in Table 5.4 are representative of a host of possible interviewers. Now we turn our attention to the situation in which the two raters can be considered to be fixed. In this case we can either ignore systematic rater differences in mean ratings, or we can adjust for them. The expression for ICR(3,1) in Table 5.3A is appropriate when we wish to describe the reliability of a single fixed rater. Unlike ICR(2,1), this version of the intraclass correlation is not affected by the between-rater mean squares. On average, ICR(3,1) will be larger in magnitude than ICR(2,1). By fixing the raters to certain persons, the extraneous variation due to sampling of raters is eliminated and the resulting reliability is usually higher. This effect is especially obvious for Z, which had a large between-rater effect. The ICR(3,1) for Z is calculated as (25.7 − 2.67)/(25.7 + (1) ∗ 2.67) = 0.81 ICR(3,1) for X is not much different than ICR(2,1), as the rater effects were small: (0.254 − 0.092)/(0.254 + (1) ∗ 0.092) = 0.47 81

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5.6.3 The reliability of the average of k fixed measures: Cronbach’s alpha Just as ICR(1,1) and ICR(2,1) can be used in the Spearman–Brown formula to determine how much reliability improves by using an average score, so can ICR(3,1) be used when an average measurement is of interest. In this case the reliability of the averaged measurement can be computed directly using ICR(3,k) from Table 5.3. For the quantitative Z variable, the reliability of the average is expected to be 0.90. One common application of ICR(3,k) is to internal consistency analyses of psychometric scales. Items in self-report questionnaires are usually fixed in that the same items are used with all respondents. Suppose that n subjects are administered k scale items, and the results are analysed using the two-way ANOVA layout of Table 5.5. The estimate of the reliability of the sum or average of the k fixed items can be computed using ICR(3,k). The result is identical to Cronbach’s alpha [12], which we discussed in the first section. Alpha is computed directly by computer programs such as SPSS RELIABILITY [35].

5.7 Other reliability statistics 5.7.1 Cohen’s kappa When binary data such as that for variable X in Table 5.4 are collected, reliability can be estimated directly using Cohen’s kappa [32]. Fleiss and Cohen [37] showed that kappa is conceptually equivalent to ICR(2,1) in Table 5.3. It can be calculated simply using the entries of a 2 × 2 table showing the diagnostic agreement. In general, this agreement table might be laid out as follows:

Rater 2: + Rater 2: − Total

Rater 1: +

Rater 1: −

Total

a c a+c

B D b+d

a+b c+d n

Cohen [32] pointed out that while cells a and d represent agreement, it is not sufficient to evaluate reliability by reporting the overall proportion of agreement, Po = (a + d)/n. This statistic may be 82

large even if raters assigned diagnoses by flipping coins or rolling dice. His kappa statistic adjusts for simple chance mechanisms: kappa =

Po − Pc 1 − Pc

where Po is the observed agreement, [(a + d)/n] and Pc is the expected agreement due to chance: Pc = [(a + c)(a + b) + (b + d)(c + d)]/n2 . When computing kappa by hand, it is sometimes more convenient to use the following equivalent expression, kappa =

ad − bc . ad − bc + n(b + c)/2

When the X data in Table 5.4 are tabulated into a 2 × 2 table like that shown above, we get a = 2, b = 2, c = 1 and d = 12. The observed agreement, Po = 0.82, but the expected agreement by chance is Pc = 0.67. Using either of the expressions for kappa, we find the reliability to be 0.46. As expected, this is quite close to the value of 0.48 obtained using ICR(2,1). One advantage of calculating the reliability of binary judgements using kappa instead of intraclass correlation methods is that the expressions for kappa’s standard error and confidence bounds are explicitly suited to binary data. Kappa can also be generalised to describe the overall reliability of classifications into multiple categories. Fleiss et al. [38] provides an overview of many forms of kappa, and Donner and his colleagues [39–44] have done much to describe the sampling variation of kappa statistics.

5.7.2 Product moment correlation If the reliability study yields two measurements, and if the raters are considered to be fixed (rather than representative of a pool of raters), then reliability can be estimated by computing the product moment correlation between the two measures. This is the usual correlation statistic built into most computer programs and calculators. When the ratings are quantitative, the correlation is known as the Pearson correlation, and when the ratings are binary it is known as the phi coefficient. Regardless of what they

RELIABILITY

are called, they are comparable to the ICR(3,1) version of the intraclass correlation described above. For the Z variables the Pearson correlation is rP = 0.83 and for the X variables in Table 5.4 the phi coefficient is rP = 0.47. These are very close to the ICR(3,1) values of 0.81 and 0.47 obtained on the same data.

5.7.3 Item response theory statistics Investigators who have a set of survey questions that are known to reflect an underlying dimension, such as severity of distress or impairment, often report estimates of Cronbach’s alpha as a summary of measurement quality. An alternate approach is to focus on the relation of each item response pattern to the underlying dimension. When items are clearly phrased and related to the underlying (latent) dimension, the probability of endorsing an item category will be systematically related to the latent dimension (see, for example [45]). Of special interest are the slope and location of each item, indicating the relevance and severity of each item with regard to the latent dimension. Item response theory (IRT) analyses are especially useful for comparing the measurement equivalence of items across different groups (e.g. [46]). Some argue that IRT analyses should supplant traditional reliability analyses (e.g. [45]).

5.8 Summary and conclusions Unreliability is a measurement problem that can often be rectified by improving interview procedures, or by using statistical sums or averages of replicate measures. Determining the extent to which unreliability is a problem, however, can be challenging. There are various designs for estimating reliability, but virtually all have some biases and shortcomings. Studies of sampling variability of reliability statistics [9, 39, 47] have suggested that sample sizes in pilot studies are often not adequate to give stable estimates about the reliability of key measurement procedures. It is important that reliability studies be considered critically in search for ways to improve measurement procedures. Specifically, if the reliability of a measure appears to be very good, ask whether there are biases in the reliability design that might bias the results optimistically. Were the respondents

sampled in the same way in the reliability study that they will be in the field study? Was the respondent given the chance to be inconsistent, or did the replication make use of archived information? If serious biases are not found, and the reliability study produced stable estimates, then one can put the issue of reliability behind you, at least for the population at hand. If the reliability of a measure appears to be poor, one should also look for biases in the reliability design. How similar were the replications? Could the poor reliability results be an artifact of legitimate changes over time, heterogeneous items within a scale, or artificially different measurement conditions? Was the sample size large enough to be sure that reliability is in fact bad? Be especially suspicious if you have evidence of validity of a measure that is purported to be unreliable. Rather than dismissing a measure with apparently poor reliability, ask whether it can be improved to eliminate noise.

References [1] American Psychiatric Association (1980) Diagnostic and Statistical Manual of Mental Disorders, 3rd edn, American Psychiatric Association, Washington, DC. [2] American Psychiatric Association (1994) Diagnostic and Statistical Manual of Mental Disorders, 4th edn, American Psychiatric Association, Washington, DC. [3] Cochran, W.G. (1968) Errors in measurement in statistics. Technometrics, 10, 637–666. [4] Snedecor, G.W. and Cochran, W.G. (1967) Statistical Methods, 6th edn, Iowa State University Press, Ames. [5] Bollen, K.A. (1989) Structural Equations with Latent Variables, John Wiley & Sons, Inc., New York. [6] Borm, G.F., Munneke, M., Lemmers, O. et al. (2007) An efficient test for the analysis of dichotomized variables when the reliability is known. Stat. Med., 26, 3498–3510. [7] Shrout, P.E. (1998) Measurement reliability and agreement in psychiatry. Stat. Methods Med. Res., 7, 301–317. [8] Lord, F.M. and Novick, M.R. (1968) Statistical Theories of Mental Test Scores, Addison-Wesley, Reading. [9] Dunn, G. (1989) Design and Analysis of Reliability Studies, Oxford University Press, New York. [10] Endicott, J., Spitzer, R.L., Fleiss, J.L. et al. (1976) The global assessment scale: a procedure for measuring overall severity of psychiatric disturbance. Arch. Gen. Psychiatry, 33, 766–771.

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CHAPTER 5 [11] Spitzer, R.L. (1983) Psychiatric diagnosis: are clinicians still necessary? Compr. Psychiatry, 24, 399–411. [12] Cronbach, L.J. (1951) Coefficient alpha and the internal structure of tests. Psychometrika, 16, 297–334. [13] McDonald, R.P. (1999) Test Theory: A Unified Treatment, Erlbaum, Mahwah. [14] Sijtsma, K. (2009) On the use, the misuse, and the very limited usefulness of Cronbach’s alpha. Psychometrika, 74 (1), 107–120. [15] Raykov, T. (1997) Scale reliability, Cronbach’s coefficient alpha, and violations of essential tauequivalence with fixed congeneric components. Multivariate Behav. Res., 32, 329–353. [16] Kraemer, H.C., Shrout, P.E. and Rubio-Stipec, M. (2007) Developing the diagnostic and statistical manual V: what will ‘statistical’ mean in DSM-5. Soc. Psychiatry Psychiatr. Epidemiol., 42 (4), 259–267. [17] Cronbach, L.J., Gleser, G.C., Nanda, H. et al. (1972) The Dependability of Behavioral Measurements: Theory of Generalizability for Scores and Profiles, John Wiley & Sons, Inc., New York. [18] Anthony, J.C., Folstein, M.,Romanoski, A.J. et al. (1985) Comparison of the lay Diagnostic Interview Schedule and a standardized psychiatric diagnosis. Arch. Gen. Psychiatry, 42, 667–675. [19] Brennan, R.L. (2001) Generalizability Theory, Springer, New York. [20] Cranford, J.A., Shrout, P.E., Iida, M. et al. (2006) A procedure for evaluating sensitivity to within-person change: can mood measures in diary studies detect change reliably? Pers. Soc. Psychol. Bull., 32 (7), 917–929. [21] Jannarone, R.J., Macera, C.A. and Garrison, C.Z. (1987) Evaluating interrater agreement through ‘casecontrol’ sampling. Biometrics, 43, 433–437. [22] Spearman, C. (1910) Correlation calculated from faulty data. Br. J. Psychol., 3, 271–295. [23] Brown, W. (1910) Some experimental results in the correlation of mental abilities. Br. J. Psychol., 3, 296–322. [24] Kraemer, H.C. (1979) Ramifications of a population model for kappa as a coefficient of reliability. Psychometrika, 44, 461–472. [25] Fleiss, J.L. and Shrout, P.E. (1989) Reliability considerations in planning diagnostic validity studies, in The Validity of Psychiatric Diagnoses (ed. L. Robbins), Guilford Press, New York, pp. 279–291. [26] Carey, G. and Gottesman, I.I. (1978) Reliability and validity in binary ratings: areas of common misunderstanding in diagnosis and symptom ratings. Arch. Gen. Psychiatry, 35, 1454–1459.

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[27] Grove, W.M., Andreason, N.C., McDonald-Scott, P. et al. (1981) Reliability studies of psychiatric diagnosis: theory and practice. Arch. Gen. Psychiatry, 38, 408–413. [28] Guggenmoos-Holzmann, I. (1993) How reliable are chance-corrected measures of agreement? Stat. Med., 12, 2191–2205. [29] Spitznagel, E.L. and Helzer, J.E. (1985) A proposed solution to the base rate problem in the kappa statistic. Arch. Gen. Psychiatry, 42, 725–728. [30] Shrout, P.E., Spitzer, R.L. and Fleiss, J.L. (1987) Quantification of agreement in psychiatric diagnosis revisited. Arch. Gen. Psychiatry, 44, 172–177. [31] Kraemer, H.C. (1992) Measurement of reliability for categorical data in medical research. Stat. Methods Med. Res., 1, 183–199. [32] Cohen, J. (1960) A coefficient of agreement for nominal scales. Educ. Psychol. Meas., 20, 37–46. [33] Blackman, N.J.-M. and Koval, J.J. (2000) Interval estimation for Cohen’s kappa as a measure of agreement. Stat. Med., 19, 723–741. [34] Walter, S.D., Eliasziw, M. and Donner, A. (1998) Sample size and optimal designs for reliability studies. Stat. Med., 17, 101–110. [35] SPSS Inc. (2009) SPSS for Windows (Version 16), SPSS Inc., Chicago. [36] Shrout, P.E. and Fleiss, J.L. (1979) Intraclass correlations: uses in assessing rater reliability. Psychol. Bull., 86, 420–428. [37] Fleiss, J.L. and Cohen, J. (1973) The equivalence of weighted kappa and the intraclass coefficient as measures of reliability. Educ. Psychol. Meas., 33, 613–619. [38] Fleiss, J.L., Levin, B. and Paik, M.C. (2003) Statistical Methods for Rates and Proportions, 3rd edn, John Wiley & Sons, Inc., New York. [39] Donner, A. (1998) Sample size requirements for the comparison of two or more coefficients of interobserver agreement. Stat. Med., 17, 1157–1168. [40] Donner, A. and Eliasziw, M. (1992) A goodnessof-fit approach to inference procedures for the kappa statistic: confidence interval construction, significancetesting and sample size estimation. Stat. Med., 11, 1511–1519. [41] Donner, A. and Eliasziw, M. (1994) Statistical implications of the choice between a dichotomous or continuous trait in studies of interobserver agreement. Biometrics, 50, 550–555. [42] Donner, A. and Eliasziw, M. (1997) A hierarchical approach to inferences concerning interobserver agreement for multinomial data. Stat. Med., 16, 1097–1106.

RELIABILITY [43] Donner, A., Eliasziw, M. and Klar, N. (1996) Testing the homogeneity of kappa statistics. Biometrics, 52, 176–183. [44] Donner, A., Shoukri, M.M., Klar, N. et al. (2000) Testing the equality of two dependent kappa statistics. Stat. Med., 19, 373–387. [45] Embretson, S.E. and Reise, S.P. (2000) Item Response Theory for Psychologists, Erlbaum, Mahwah.

[46] Gregorich, S.E. (2006) Do self-report instruments allow meaningful comparisons across diverse population groups? Med. Care, 44 (11), S78–S94. [47] Cantor, A.B. (1996) Sample-size calculations for Cohen’s kappa. Psychol. Methods, 1, 150–155.

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Moderators and mediators: Towards the genetic and environmental bases of psychiatric disorders Helena Chmura Kraemer Department of Psychiatry, Stanford University, CA, USA and University of Pittsburgh, Pittsburgh, PA, USA

6.1 Introduction The terms ‘moderator’ and ‘mediator’ have been around for at least 50 years, but until 1986, the terms were used inconsistently and idiosyncratically. As a result, the constructs of moderation/mediation played little role in biomedical research. In 1986 [1] Baron and Kenny proposed conceptual definitions to distinguish moderators from mediators, giving each term a specific distinct meaning. According to those conceptual definitions, when M (moderator or mediator), T (target variable) and O (outcome variable) are three variables measured on the individual subjects in a population: • M moderates the effect of T on O if M helps explain on whom or under what conditions T leads to O. • M mediates the effect of T on O if M helps to explain why or how T leads to O. Baron and Kenny also proposed a statistical method to apply those definitions, based on a linear model, assuming that the outcome is determined by a linear function of T and M: Linear Model: β0 + β1 T + β2 M + β3 TM

To show moderation Baron and Kenny required only that it be shown that β3 = 0. That is problematic, for a demonstration that T moderates M also demonstrates that M moderates T, leaving the direction of moderation ambiguous. To show mediation, they required that the interaction effect be assumed to be zero. That too is problematic, for if interaction exists in the population but is assumed zero in the model, that effect is remapped partially into the other coefficients, biasing them, and partially into the error, reducing power. Moreover, users were encouraged to fit both models to one set of data, first proving a non-zero interaction to show moderation, and then illogically assuming a zero interaction to show mediation, leading to a conclusion that one variable can both moderate and mediate another in its effect on the outcome. Added to such problems intrinsic to the approach, many users began to refer to any interactive relationship as ‘moderation’, to use the term ‘mediator’ as synonymous with ‘cause’, or to refer to a variable as a ‘moderator’ or a ‘mediator’ without specifying what the target and/or the outcome was. These are all misuses of the Baron and Kenny definitions. Around 2000, a subgroup of the MacArthur Network on Psychopathology in Development, modified

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the Baron and Kenny criteria [2, 3], retaining their conceptual definitions, but attempting to set criteria to resolve and clarify the incongruities and ambiguities [4]. This approach, the so-called MacArthur approach, is discussed here. The MacArthur reformulation clarified the importance of the moderator/mediator concept to all biomedical research, particularly psychiatry. Moderators of treatment on outcome in randomised clinical trials (RCTs) identify subpopulations that respond differently to treatments, facilitating personalisation in the form of targeting of treatment choices to those most benefited [3, 5–7]. Mediators of treatments in RCTs suggest ways in which a treatment might be made more effective or more cost-effective, thus encouraging personalisation in the form of tailoring treatment to individual needs [5]. Similarly in risk research, there may be chains of mediators leading to onset of a disorder (some perhaps causal), and even multiple such chains in subpopulations defined by moderators of those risk factors on that disorder [8, 9]. In the present discussion the moderator/mediator approach specifically directed to understanding the genetic influences on disorders will be discussed. Consider the simple situation in which G represents the presence (G = 1) or absence (G = 0) of a certain genotype, and E represents some binary factor (E = 1 and 0) such as presence/absence of an environmental factor, a gene expression or its effect on the individual, or an event, all during the early lifetime of an individual, where both G and E are risk factors for the disorder D. D represents whether the individual experiences the onset of a disorder (D+) or not (D−) at a certain time point (prevalence) or during a certain time span (incidence) in later lifetime. The complete distribution of (G, E, D) in the population is described in Table 6.1 There is nothing in the moderator/mediator approach that requires that the three variables be binary, but the basic concepts are clearest in this simple situation and thereafter easily expanded to more general situations. To motivate this discussion, consider first an extreme special case: Suppose that the only individuals who have D+ are those with both G = 1 and E = 1 (P11 = 1, Pij = 0 otherwise). If G and E were simultaneously studied, in the population of interest, the risk difference (RD) between those with both G 88

Table 6.1 G and E binary risk factors for the disorder D, with G (genotype) temporally preceding E (environmental risk factor, genetic expression, event), preceding D. G

E

Probability of (G, E) in the population

Probability of D+

1 1 0 0

1 0 1 0

pq1 p(1 − q1 ) (1 − p)q2 (1 − p)(1 − q2 )

P11 P10 P01 P00

and E = 1 and others would be a perfect 1.00. It would take a very small sample from the population to detect what the situation is. However, if one studied only the genotype, the probability of the disorder in the G = 1 subgroup is q1 , and that in the G = 0 subgroup is 0, a RD now of q1 < 1. If, as often happens, E = 1 is rare (q1 near zero), that represents considerable attenuation of the effect size. Moreover, the disorder itself cannot be observed; only a diagnosis of the disorder, which has a certain sensitivity (SED ) and specificity (SPD ) for that disorder, that is almost never perfect. Then when only G is considered, the RD is an even more attenuated q1 (SED + SPD − 1). To detect such an attenuated association, the sample size may have to be very large, and even if such association were found ‘statistically significant’, the effect size might well appear trivial. A great deal of attention has been focused on improving the reliability of measurement of G, E and especially of D for psychiatric disorders, but until recently, little attention has been paid to the fact that if genes and environment ‘work together’ in their effect on a disorder, studying genes in absence of the environment, (or environment in absence of genes), may conceal the crucial role that both genes and environment play in the aetiology of disorders. In what follows, the sample is assumed to be a representative one from the population of interest. G, E and D are binary, as reliably measured as possible. Their errors of measurement are independent of each other, an assumption that can be guaranteed in design by ‘blinding’ each assessment to the others. Based on these assumptions, several methodological problems are discussed, that are barriers to resolving such issues, necessary to clarifying the MacArthur moderator/mediator approach

Textbook in Psychiatric Epidemiology, Third Edition. Edited by Ming T. Tsuang, Mauricio Tohen and Peter B. Jones © 2011 John Wiley & Sons, Ltd. ISBN: 978-0-470-69467-1

MODERATORS AND MEDIATORS: TOWARDS THE GENETIC AND ENVIRONMENTAL BASES OF PSYCHIATRIC DISORDERS

for considering the genetic/environmental bases of psychiatric disorders. Then moderation and mediation as well as other important ways in which multiple factors can ‘work together’ to explain an outcome are defined. The concept is then expanded from one binary variable at each of three time points, to one variable measured at any level at each of three time points, to multiple variables at each of three time points, to multiple variables at multiple time points. The goal is to suggest how, using these principles, one might ‘piece together’ a very complex picture of what might lead to a disorder, thus to suggest how complex disorders might be prevented or successfully treated.

6.2 Current methodological barriers 6.2.1 Case–control studies Case–control studies are one of the most common approaches to examining the genetic bases of a disorder. It is very difficult in population-based studies to generate a sufficient number of cases of the disorder (D+) in a prospective study, when the disorder of interest is, as it often is, quite rare. A favoured alternative has long been to do a retrospective case–control study, in which N1 subjects are sampled from among those who have already had onset of the disorder of interest, and N2 subjects from among those without that disorder. In a case–control study, clearly genotype can be as reliably and accurately measured on the total sample after onset of the disorder as it might have been prospectively before the onset of the disorder. Accurate measurement of environment, gene expression, or events prior to onset of the disorder, however, is very difficult. Memory is flawed, records are often incomplete, and, most important, recall is often coloured by the subject’s knowledge that they do or do not have the disorder in question at the time of assessment. Moreover, Berkson’s Fallacy has been known since the 1950s [10, 11]: The samples of ‘cases’ and ‘controls’ may not be representative of the cases or the controls that would have resulted in prospective study of a population for a variety of reasons. What one sees in a case–control study may

well misrepresent what would have been seen in a prospective study of the same risk factors and outcomes in the same population. In short, while the first studies to explore associations between risk factors and outcomes may well be case–control studies, accepting inferences from such studies as ‘scientific truth’ is risky. Instead, such studies should be used to generate strong hypotheses to be tested in subsequent prospective studies, and to yield the information necessary to design powerful and cost-effective such prospective studies. The type of study design necessary to understanding gene moderation or mediation corresponds to the third type of study design discussed by Fitzmaurice and Ravichandran (Chapter 2), in which a random number of subjects are sampled from a population and both binary characteristics are measured on each subject.

6.2.2 Statistical significance necessary but not sufficient Concepts related to statistical hypothesis testing, such as ‘significance level’, ‘p-values’, ‘power’, came into common use in biomedical research about midtwentieth century. In recent years, however, there is a growing realisation of the limitations of statistical hypothesis testing [12–18]. One prominent epidemiological journal actually banned the use of ‘p-values’ for a time, while psychology [14, 19] and medicine [20–22] tried to deal with the problem by urging that every p-value be accompanied by a clinically interpretable effect size and its confidence interval. In the way such testing is commonly done (testing null hypotheses of randomness), ‘statistically significant’ generally means that the data are sufficient to demonstrate a non-random association, a comment on the data, not on the strength of association. Any non-null association, no matter how trivial, can be shown to be ‘statistically significant’ provided the sample size is large enough. The crucial issue is whether the strength of association is enough to warrant further interest in that association. In dealing with how risk factors ‘work together’ in the MacArthur approach, effect sizes are decomposed to understand the contributions of various risk factors. In essence, this approach assumes that, when there is rationale and justification for suspecting an 89

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association between G and D, most, if not all, effect sizes are non-null, although many, perhaps most, may be trivial. Certainly in all research into the risk factors (genetic or otherwise) for a disorder, it is necessary to establish statistical significance to warrant drawing any conclusions. It is not sufficient to stop there: a clinically interpretable effect size is necessary.

6.2.3 Odds ratio is not a clinically interpretable effect size The most common effect size used in epidemiological and genetic research is the odds ratio. If the probability of D+ in the high risk group is Q1 and that in the low risk group is Q0 , the odds of D+ in the two groups are Q1 /(1 − Q1 ) and Q0 /(1 − Q0 ). The odds ratio (OR) is the ratio of those two odds. The odds ratio was originally introduced as the likelihood ratio test statistic to test the null hypothesis of random differences between the two groups (Q1 = Q0 ), and remains an excellent indicator of non-randomness [23]. OR = 1 means that Q1 = Q0 ; OR = 1 indicates non-random association. Use of the odds ratio to test for non-random association, for example using logistic regression analysis, is both common and recommended. However, there are a number of arguments against the odds ratio as an interpretable effect size [23–27] all converging on one conclusion: odds ratio should not be used as an effect size, but only as an indicator of nonrandomness. Consider three questions: If not the odds ratio, then what? Why the odds ratio? Why not the odds ratio? If not the odds ratio, then what? What has been shown is that, once one excludes the odds ratio from consideration, all the other common measures of 2 × 2 association correspond to one or another of the weighted kappa coefficients [25]. Which weighted kappa is appropriate in any given situation depends on the relative clinical importance of false positives to false negatives (which determines the weight in the weighted kappa). Thus among commonly used measures of 2 × 2 association, odds ratio is an outlier. For the purpose of the pr