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151.3.3 Methods Using the Treatment Assignment Mechanism and the Outcome.. The scope of methods considered are limited tolinear outcome models—a single treatment assignment mechanism mod

Comparative Effectiveness Research

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Byron Jones, Biometrical Fellow, Statistical Methodology, Integrated Information Sciences, Novartis Pharma AG, Basel, Switzerland

Jen-pei Liu, Professor, Division of Biometry, Department of Agronomy,

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Theory of Drug Development

Comparative Effectiveness Research

Edited by Constantine Gatsonis

Brown University, Providence, Rhode Island, USA

Sally C Morton

Virginia Tech, Blacksburg, Virginia, USA

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Names: Gatsonis, Constantine, editor | Morton, Sally C., editor.

Title: Methods in comparative effectiveness research / Constantine Gatsonis,

Sally C Morton.

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Identifiers: LCCN 2016039233 | ISBN 9781466511965 (hardback)

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Contributors xiIntroduction xv

1 An Overview of Statistical Approaches for Comparative

Effectiveness Research .3

Lauren M Kunz, Sherri Rose, Donna Spiegelman,

and Sharon-Lise T Normand

2 Instrumental Variables Methods 39

Michael Baiocchi, Jing Cheng, and Dylan S Small

3 Observational Studies Analyzed Like Randomized Trials

and Vice Versa 107

Miguel A Hernán and James M Robins

Section II Clinical Trials: Design, Interpretation,

7 Combining Information from Multiple Data Sources: An

Introduction to Cross-Design Synthesis with a Case Study 203

Joel B Greenhouse, Heather D Anderson, Jeffrey A Bridge, Anne

M Libby, Robert Valuck, and Kelly J Kelleher

ix

8 Heterogeneity of Treatment Effects 227

Issa J Dahabreh, Thomas A Trikalinos, David M Kent,

and Christopher H Schmid

9 Challenges in Establishing a Hierarchy of Evidence 273

Robert T O’Neill

10 Systematic Reviews with Study-Level and Individual

Patient-Level Data 301

Joseph Lau, Sally C Morton, Thomas A Trikalinos,

and Christopher H Schmid

11 Network Meta-Analysis 341

Orestis Efthimiou, Anna Chaimani, Dimitris Mavridis,

and Georgia Salanti

12 Bayesian Network Meta-Analysis for Multiple Endpoints 385

Hwanhee Hong, Karen L Price, Haoda Fu, and Bradley P Carlin

13 Mathematical Modeling 409

Mark S Roberts, Kenneth J Smith, and Jagpreet Chhatwal

14 On the Use of Electronic Health Records 449

Sebastien J-P.A Haneuse and Susan M Shortreed

15 Evaluating Personalized Treatment Regimes 483

Eric B Laber and Min Qian

16 Early Detection of Diseases 499

Sandra Lee and Marvin Zelen

17 Evaluating Tests for Diagnosis and Prediction 519

Constantine Gatsonis

Index 535

The Research Institute at

Nationwide Children’s Hospital

Department of Preventive and

Restorative Dental Science

UCSF School of Dentistry

San Francisco, California

Constantine Gatsonis

Department of BiostatisticsBrown University School ofPublic Health

Providence, Rhode Island

Joel B Greenhouse

Department of StatisticsCarnegie Mellon UniversityPittsburgh, Pennsylvania

Sebastien J-P.A Haneuse

Department of BiostatisticsHarvard Chan School of PublicHealth

Boston, Massachusetts

xi

Department of Mental Health

Johns Hopkins University

Baltimore, Maryland

Kelly J Kelleher

The Research Institute at

Nationwide Children’s Hospital

Office of Biostatistics Research

National Heart, Lung, and Blood

North Carolina State University

Raleigh, North Carolina

Providence, Rhode Island

Sandra Lee

Department of Biostatisticsand ComputationalBiology

Dana-Farber Cancer Instituteand Harvard MedicalSchool

andDepartment of BiostatisticsHarvard T.H Chan School ofPublic Health

Boston, Massachusetts

Anne M Libby

Department of EmergencyMedicine

University of ColoradoAurora, Colorado

Ioannina, Greece

Sally C Morton

College of Science and Department

of StatisticsVirginia TechBlacksburg, Virginia

Office of Translational Sciences

Center for Drug Evaluation and

University of BernBern, Switzerland

Christopher H Schmid

Department of BiostatisticsCenter for Evidence Synthesis inHealth

Brown University School ofPublic Health

Providence, Rhode Island

Susan M Shortreed

Biostatistics UnitGroup Health Research InstituteSeattle, Washington

Dylan S Small

Department of StatisticsThe Wharton School of theUniversity of PennsylvaniaPhiladelphia, Pennsylvania

Kenneth J Smith

Department of MedicineSchool of MedicineUniversity of PittsburghPittsburgh, Pennsylvania

Donna Spiegelman

Departments of Epidemiology,Biostatistics, and NutritionHarvard T.H Chan School ofPublic Health

Boston, Massachusetts

Elizabeth A Stuart

Department of Mental HealthJohns Hopkins UniversityBaltimore, Maryland

Thomas A Trikalinos

Department of Health Services,

Policy and Practice

Center for Evidence Synthesis in

Boston, Massachusetts

What Is Comparative Effectiveness Research?

Comparative effectiveness research (CER) has emerged as a major nent of health care and policy research over the past two decades Severaldefinitions of CER have been proposed The most widely used is the defini-tion provided by the Institute of Medicine (IOM; now the National Academy

compo-of Medicine) committee convened to define national priorities for CER in

2009 According to this definition, “Comparative effectiveness research (CER)

is the generation and synthesis of evidence that compares the benefits andharms of alternative methods to prevent, diagnose, treat, and monitor a clin-ical condition or to improve the delivery of care” [1] According to the IOMreport, CER is conducted in order to develop evidence that will aid patients,clinicians, purchasers, and health policy makers in making informed deci-

sions The overarching goal is to improve health care at both the individual and

population levels.

Insofar as the focus of CER is on effectiveness, the contrast with efficacy needs

to be made Efficacy refers to the performance of a medical intervention

under “ideal” circumstances, whereas effectiveness refers to the performance

of the intervention in “real-world” clinical settings With efficacy and tiveness defining the two ends of a continuum, actual studies typicallyoccupy one of the intermediate points However, effectiveness trials areexpected to formulate their aims and design based on the realities of routineclinical practice and to assess outcomes that are directly relevant to clinicaldecisions Such trials are often termed “pragmatic clinical trials” in the CERlexicon [2]

effec-In order to maintain the focus on effectiveness, CER studies involve lations that are broadly representative of clinical practice CER also calls forcomparative studies, including two or more alternative interventions withthe potential to be the best practice and assessing both harms and bene-fits CER studies often involve multiple arms and rarely include placebo

popu-arms Importantly, CER aspires to focus on the individual rather than the

average patient As a result, the goal of CER is to develop as granular

information as possible, in order to assist medical decision making for viduals Comparative results on subgroups are very important in the CERcontext

indi-xv

Patient-Centered Research and PCORI

Among several entities that promote and fund studies of comparativeeffectiveness, a central role was given to the Patient-Centered OutcomesResearch Institute (PCORI) This institute, a public–private partnership,was established and funded by the Patient Protection and Affordable CareAct (PPACA) to conduct CER and generate information needed for healthcare and policy decision making under PPACA PCORI developed its ownformulation of CER with an emphasis on patient-centeredness In this for-mulation, an overarching goal of CER is to provide information that willaddress the following main questions faced by patients: (a) Given my per-sonal characteristics, conditions, and preferences, what should I expect willhappen to me? (b) What are my options, and what are the potential bene-fits and harms of those options? (c) What can I do to improve the outcomesthat are most important to me? (d) How can clinicians and the healthcaredelivery systems they work in help me make the best decisions about myhealth and health care? [3] An important caveat here is that the class ofpatient-centered outcomes is not the same as the class of patient-reportedoutcomes In addition, PCORI asks that studies include a wide array of stake-holders besides patients, including family members, informal and formalcaregivers, purchasers, payers, and policy makers, but the patient remainsthe key stakeholder

Evolution of CER

As Greenfield and Sox noted in summarizing the IOM CER CommitteeReport, “Research that informs clinical decisions is everywhere, yet a nationalresearch initiative to improve decision making by patients and their physi-cians is a novel concept” [4] Healthcare reform, and particularly the estab-lishment of PCORI and consequently targeted funding, accentuated CER.Notably, funding related to CER is not restricted to PCORI Other agen-cies have adopted the CER paradigm in funding announcements and alsorecommend the involvement of stakeholders in studies [5]

CER has evolved in the 6 years since healthcare reform Researchers andthe patient advocacy community are designing and conducting CER studies,

as well as developing the methodology to conduct such studies The PCORIlegislation required that methodological standards for conducting CER beestablished by the PCORI Methodology Committee Forty-seven standardswere constructed [6], with a current revision ongoing These standards haveincreased the attention on methods, and the quality of CER studies Method-ological work is especially focused on trial design, for example, adaptive

designs, as well as causal inference in the observational setting As discussed

in the next section, this book addresses these methodological issues andmore

The scientific literature has responded with several special issues devoted

to CER, including Health Affairs in October 2010 and the Journal of the American

Medical Association (JAMA) in April 2012 A journal devoted to CER, the nal of Comparative Effectiveness Research, was established in 2012 The renewed

Jour-focus on causal inference has increased methodological work and resulted in

new journals as well, including Observational Studies, established in 2015.

In terms of data availability, particularly for the conduct of large matic trials, PCORI has funded the construction of a national clinical dataresearch network PCORnet to facilitate the analysis of electronic healthrecords (EHRs) and claims [7] Funding for training and education is nowavailable, particularly via the Agency for Healthcare Research and Qual-ity (AHRQ), which receives a portion of PCORI funding for such activities.AHRQ has funded a K12 Scholars Program on patient-centered outcomesresearch, for example The interested reader may also wish to take advantage

prag-of the methodology standards curriculum [8] and the continuing medicaleducation material [9] available at PCORI Dissemination and implementa-tion of CER results are still in their infancy, though the spotlight has nowturned to these essential next steps

Scope and Organization of This Book

CER encompasses a very broad range of types of studies In particular, ies of comparative effectiveness can be experimental, notably randomized-controlled trials, or observational The latter can be prospective studies, forexample, involving registries and EHR databases, or postmarketing safetystudies They can also be retrospective, for example, involving the analy-sis of data from healthcare claims Research synthesis occupies a significantplace in CER, including the conduct of systematic reviews and meta-analyses.The use of modeling is increasingly important in CER given CER’s focus ondecision making, including decision analysis and microsimulation modeling.Although the legal framework of PCORI does not cover cost-effectivenessanalysis, the area is an important dimension of CER in the eyes of many inthe research and health policy communities

stud-The choice of material and organization of this book is intended to coverthe main areas of methodology for CER, to emphasize those aspects that areparticularly important for the field, and to highlight their relevance to CERstudies Although the coverage of topics is not encyclopedic, we believe thisbook captures the majority of important areas

The book is organized into four major sections The first three cover thefundamentals of CER methods, including (I) Causal Inference Methods,(II) Clinical Trials, and (III) Research Synthesis The fourth section is devoted

to more specialized topics that round out the book Each section containsseveral chapters written by teams of authors with deep expertise and exten-sive track record in their respective areas The chapters are cross-referencedand provide an account of both theoretical and computational issues, alwaysanchored in CER domain research The chapter authors provide additionalreferences for further study

The book is primarily addressed to CER methodologists, quantitativetrained researchers interested in CER, and graduate students in all branches

of statistics, epidemiology, and health services and outcomes research Theintention is for the material to be accessible to anyone with a masters-levelcourse in regression and some familiarity with clinical research

Acknowledgments

We thank our chapter authors and our publisher, particularly John Kimmel,for their contributions and patience We thank our institutions, Brown Uni-versity and Virginia Tech, and Dr Morton’s prior institution, the University

of Pittsburgh, respectively, for their support We hope that this book will helppatients and their families make better healthcare decisions

Constantine Gatsonis and Sally C Morton

4 Sox HC, Greenfield S Comparative effectiveness research: A report from the

Institute of Medicine Ann Intern Med 2009;151(3):203–5.

5 Burke JG, Jones J, Yonas M, Guizzetti L, Virata MC, Costlow M, Morton SC,Elizabeth M PCOR, CER, and CBPR: Alphabet soup or complementary fields

of health research? Clin Transl Sci 2013;6(6):493–6 doi: 10.1111/cts.12064 Epub

May 8, 2013

6 PCORI (Patient-Centered Outcomes Research Institute) Methodology tee The PCORI Methodology Report, 2013, http://www.pcori.org/research-we-support/research-methodology-standards, accessed April 12, 2016

Commit-7 Fleurence RL, Curtis LH, Califf RM, Platt R, Selby JV, Brown JS Launching

PCORnet, a national patient-centered clinical research network J Am Med Inform

Assoc 2014;21(4):578–82 doi: 10.1136/amiajnl-2014-002747 Epub May 12, 2014.

8 standards-academic-curriculum, accessed April 12, 2016

http://www.pcori.org/research-results/research-methodology/methodology-9 http://www.pcori.org/research-results/cmece-activities, accessed April 12,2016

Causal Inference Methods

An Overview of Statistical Approaches for Comparative Effectiveness Research

Lauren M Kunz, Sherri Rose, Donna Spiegelman,

and Sharon-Lise T Normand

CONTENTS

1.1 Introduction 41.2 Causal Model Basics 51.2.1 Parameters 71.2.2 Assumptions 81.2.2.1 Stable Unit Treatment Value Assignment: No

Interference and No Variation in Treatment 91.2.2.2 Ignorability of Treatment Assignment 91.2.2.3 Positivity 101.2.2.4 Constant Treatment Effect 101.3 Approaches 111.3.1 Methods Using the Treatment Assignment Mechanism 111.3.1.1 Matching 121.3.1.2 Stratification 131.3.1.3 Inverse Probability of Treatment Weighted (IPTW)

Estimators 131.3.2 Methods Using the Outcome Regression 141.3.2.1 Multiple Regression Modeling 141.3.2.2 G-Computation 151.3.3 Methods Using the Treatment Assignment Mechanism

and the Outcome 161.3.3.1 Augmented Inverse Probability Weighted

Estimators 161.3.3.2 Targeted Maximum Likelihood Estimator 161.4 Assessing Validity of Assumptions 171.4.1 SUTVA 171.4.2 Ignorability 181.4.3 Positivity 181.4.4 Constant Treatment Effect 191.5 Radial versus Femoral Artery Access for PCI 19

3

1.5.1 Estimating Treatment Assignment: Probability of Radial

Artery Access 191.5.2 Approaches 221.5.2.1 Matching on the Propensity Score 231.5.2.2 Stratification on the Propensity Score 231.5.2.3 Weighting by the Propensity Score 261.5.2.4 Multiple Regression 261.5.2.5 G-Computation 271.5.2.6 Augmented IPTW 271.5.2.7 Targeted Maximum Likelihood Estimation 271.5.3 Comparison of Approaches 271.6 Concluding Remarks 30Acknowledgments 31Appendix 1A.1: Implementing Methods for Comparative Effectiveness

Research 31References 35

ABSTRACT This chapter reviews key statistical tenets of comparativeeffectiveness research with an emphasis on the analysis of observationalcohort studies The main concepts discussed relate to those for causal anal-ysis whereby the goal is to quantify how a change in one variable causes achange in another variable The methodology for binary treatments and a sin-gle outcome are reviewed; estimators involving propensity score matching,stratification, and weighting; G-computation; augmented inverse probabil-ity of treatment weighting; and targeted maximum likelihood estimation arediscussed A comparative assessment of the effectiveness of two differentartery access strategies for patients undergoing percutaneous coronary inter-ventions illustrates the approaches Rudimentary R code is provided to assistthe reader in implementing the various approaches

1.1 Introduction

Comparative effectiveness research (CER) is designed to inform healthcaredecisions by providing evidence on the effectiveness, benefits, and harms ofdifferent treatment options [1] While the typology of CER studies is broad,this chapter focuses on CER conducted using prospective or retrospectiveobservational cohort studies where participants are not randomized to anintervention, treatment, or policy We assume outcomes and covariates aremeasured for all subjects and there is no missing outcome or covariate infor-mation throughout; we also assume that the data are sampled from the targetpopulation—the population of all individuals for which the treatment may

be considered for its intended purpose Without loss of generality, we usethe terms “control” and “comparator” interchangeably and focus on one

nontime-varying treatment The scope of methods considered are limited tolinear outcome models—a single treatment assignment mechanism modeland a single linear outcome model.

An example involving the in-hospital complications of radial artery accesscompared to femoral artery access in patients undergoing percutaneous coro-nary interventions (PCI) illustrates ideas Coronary artery disease can betreated by a PCI in which either a balloon catheter or a coronary stent is used

to push the plaque against the walls of the blocked artery Access to the nary arteries via the smaller radial artery in the wrist, rather than the femoralartery in the groin, requires a smaller hole and may, therefore, reduce access-site bleeding, patient discomfort, and other vascular complications Table 1.1summarizes information for over 40,000 adults undergoing PCI in all nonfed-eral hospitals located in Massachusetts The data are prospectively collected

coro-by trained hospital data managers utilizing a standardized collection tool,sent electronically to a data coordinating center, and adjudicated [2] Base-line covariates measured include age, sex, race, health insurance information,comorbidities, cardiac presentation, and medications given prior to the PCI.Overall, radial artery access (new strategy) compared to femoral artery access(standard strategy) is associated with fewer in-hospital vascular and bleed-ing complications (0.69% vs 2.73%) However, there is significant treatmentselection—healthier patients are more likely to undergo radial artery accesscompared to those undergoing femoral artery access Patients associatedwith radial artery access have less prior congestive heart failure, less leftmain coronary artery disease, and less shock compared to those undergoing

femoral artery access The CER question is: When performing PCI, does radial

artery access cause fewer in-hospital complications compared to femoral artery access for patients with similar risk?

The remainder of the chapter provides the main building blocks foranswering CER questions in settings exemplified by the radial artery accessexample—a single outcome with two treatment options We sometimesrefer to the two treatment groups as treated and comparator, exposed andunexposed, or treated and control Notation is next introduced and the statis-

tical causal framework is described We adopt a potential outcomes framework

to causal inference [3] The underlying assumptions required for CER are cussed We restrict our focus to several major classes of estimators, and notethat we do not exhaustively include all possible estimators for our parameter

dis-of interest Approaches for assessing the validity dis-of the assumptions followand methods are illustrated here using the PCI data

1.2 Causal Model Basics

Assume a population of N units indexed by i each with an outcome, Y i

In the radial artery example, units are subjects, and Y i = 1 if subject i had

Note: All entries are percentages with the exceptions of number of

observations, age, and number of vessels with>70% stenosis.

TABLE 1.2

Notation for the Potential Outcomes Framework to Causal Inference

T i Binary treatment for unit i (1 = treatment; 0 = comparator)

Y 0i Potential outcome for unit i if T i= 0

Y 1i Potential outcome for unit i if T i= 1

X i Vector of pretreatment measured covariates for person i

μT E X (E(Y | T = t, X)), marginal expected outcome under t

a complication after PCI and 0 otherwise Assume a binary-valued

treat-ment such that T i = 1 if the patient received the new treatment (e.g., radialartery access) and 0 (e.g., femoral artery access) otherwise Approaches for

treatments assuming more than two values, multivalued treatments,

gener-alize from those based on binary-valued treatments (see References 4 and5) Variables that are not impacted by treatment level and occur prior to

treatment assignment are referred to as covariates Let X i denote a vector ofobserved covariates, all measured prior to receipt of treatment The notation

is summarized in Table 1.2 Confounding occurs due to differences in the come between exposed and control populations even if there was no expo-sure The covariates that create this imbalance are called confounders [6]

out-Another type of covariate is an instrumental variable that is independent of

the outcome and correlated with the treatment (see Reference 7) A detaileddiscussion of methods for instrumental variables is provided in Chapter 2.Instrumental variables, when available, are used when important key con-founders are unavailable; their use is not discussed here In the radial arteryexample, X includes age, race, sex, health insurance information, and cardiacand noncardiac comorbidities Because there are two treatment levels, thereare two potential outcomes for each subject [8] Only one of the two potentialoutcomes will be observed for a unit

1.2.1 Parameters

The idea underpinning a causal effect involves comparing what the

out-come for unit i would have been under the two treatments—the potential

outcomes Let Y 1i represent the outcome for unit i under T i = 1 and Y0i for

Ti = 0 The causal effect of the treatment on the outcome for unit i can be defined in many ways For instance, interest may center on an absolute effect,

i = Y 1i − Y 0i , the relative effect, i = Y1i /Y 0i, or on some other function ofthe potential outcomes The fundamental problem of causal inference is that

we only observe the outcome under the actual treatment observed for unit i,

Y i = Y 0i (1 − T i ) + Y 1i (T i ) A variety of causal parameters are available with

the choice dictated by the particular problem We focus on the causal meter on the difference scale,  = μ1− μ0, where μ1 and μ0 represent thetrue proportions of complications if all patients had undergone radial arteryaccess and femoral artery access, respectively The marginal mean outcome

para-under treatment T = t is defined as

μT = E X (E(Y | T = t, X)) , (1.1)

averaging over the distribution of X The marginal expected outcome is found by examining the conditional outcome given particular values of X and averaging the outcome over the distribution of all values of X The

parameterμT is useful when interest rests on assessing population tions If the treatment effect is constant or homogeneous, then the marginalparameter is no different from the conditional parameter

interven-The average treatment effect (ATE) is defined as

E[Y1− Y0]= E X (E[Y | T = 1, X = x] − E[Y | T = 0, X = x]) (1.2)and represents the expected difference in the effect of treatment on the out-come if subjects were randomly assigned to the two treatments The ATEincludes the effect on subjects for whom the treatment was not intended, andtherefore may not be relevant in some policy evaluations [9] For example, toassess the impact of a food voucher program, interest rests on quantifying the

effectiveness of the program for those individuals who are likely to participate

in the program In this case, the causal parameter of interest is the averageeffect of treatment on the treated (ATT)

EX (E[Y | T = 1, X = x] − E[Y | T = 0, X = x] | T = 1) (1.3)The ATT provides information regarding the expected change in the outcomefor a randomly selected unit from the treatment group

Which causal estimand is of interest depends on the context When domized, on average, the treated sample will not be systematically differentfrom the control sample, and the ATT will be equal to the ATE Through-out this chapter, we focus on the ATE as the causal estimand of interestbecause (1) both radial and femoral artery access are a valid strategy for allsubjects undergoing PCI and (2) we wish to determine whether fewer com-plications would arise if everyone had undergone radial artery access ratherthan femoral artery access

ran-1.2.2 Assumptions

The foremost is the explicit assumption of potential outcomes The ability tostate the potential outcomes implies that although an individual receives aparticular treatment, the individual could have received the other treatment,and hence has the potential outcomes under both treatment and comparisonconditions

1.2.2.1 Stable Unit Treatment Value Assignment: No Interference

and No Variation in Treatment

The stable unit treatment value assignment (SUTVA) consists of two parts:(1) no interference and (2) no variation in treatment SUTVA is untestable andrequires subject matter knowledge The no interference assumption impliesthat the potential outcomes for a subject do not depend on treatment assign-ments of other subjects In the radial artery example, we require that radialartery access in one subject does not impact the probability of an in-hospitalcomplication in another subject If a subject’s potential outcomes depend on

treatments received by others, then Y i (T1, T2, , TN), indicating the outcome

for subject i, depends on the treatment received by T1, T2, , TN SUTVAimplies

Y i (T1, T2, , TN) = Y i (T i ) = Y it (1.4)Under what circumstances would the assumption of no interference be vio-lated? Consider determining whether a new vaccine designed to preventinfectious diseases—because those who are vaccinated impact whether oth-ers become infected, there will be interference The radial artery accessexample may violate the no interference assumption when considering the

practice makes perfect hypothesis As physicians increase their skill in

deliver-ing a new technology, the less likely complications arise in subsequent uses,and the more likely the physician is to use the new technology Condition-ing physician random effects would make the no interference assumptionreasonable

The second part of SUTVA states that there are not multiple versions of thetreatment (and of the comparator), or that the treatment is well defined andthe same for each subject receiving it In the radial artery access example, ifdifferent techniques are used to access the radial artery (or the femoral artery)

by different clinicians, then the SUTVA is violated

1.2.2.2 Ignorability of Treatment Assignment

The most common criticism of CER using observational cohort studiesinvolves the unmeasured confounder problem—the assertion that an unmea-sured variable is confounding the relationship between treatment and

the outcome Ignorability of the treatment assignment or unconfoundedness

of the treatment assignment with the outcome assumes that conditional

on observed covariates, the probability of treatment assignment does notdepend on the potential outcomes Hence, treatment is effectively ran-domized conditional on observed baseline covariates This assumption isuntestable and can be strong, requiring observation of all variables that affectboth outcomes and treatment in order to ensure

(Y0, Y1) ⊥ T | X and P(T = 1 | Y0, Y1, X ) = P(T = 1 | X). (1.5)

In the radial artery access example, ignorability of treatment assignmentmay be violated if someone with subject matter knowledge demonstratedthat we had omitted a key covariate from Equation 1.1 that is associated withthe probability of receiving radial versus femoral artery access, as well asin-hospital complications For instance, if knowledge regarding whether thepatient experienced an ST-segment elevated MI (STEMI) prior to the PCI wasnot collected, then differences in outcomes between the two access strategiescould be due to STEMI.

If the previous assumptions of SUTVA and ignorability of treatment assignment are violated, the causal parameters can be estimated statistically, but cannot be inter- preted causally The remainder of the assumptions can be statistically assessed (see Section 1.4).

cer-of males Practical violations cer-of the positivity assumption may arise due tofinite sample sizes With a large number of covariates, there may not be sub-jects receiving treatment and control in strata induced by the covariate space.Positivity is a statistically testable assumption

1.2.2.4 Constant Treatment Effect

A constant treatment effect conditional on X implies that for any two

sub-jects having the same values of covariates, their observable treatment effectsshould be similar:

Under a constant treatment effect, the ATE may be interpreted bothmarginally and conditionally While this assumption can be empiricallyassessed, guidelines regarding exploratory and confirmatory approaches todetermination of nonconstant treatment effects should be consulted (seeReference 10)

1.3 Approaches

Under the assumptions described above, various approaches exist to mate the ATE The approaches are divided into three types: methods thatmodel only the treatment assignment mechanism via regression, methodsthat model only the outcome via regression, and methods that use both thetreatment assignment mechanism and outcome Formulae are provided andgeneral guidelines for implementation based on existing theory to assist thereader in deciding how best to estimate the ATE are described

esti-1.3.1 Methods Using the Treatment Assignment Mechanism

Rosenbaum and Rubin [11] defined the propensity score as the probability

of treatment conditional on observed baseline covariates, e (Xi ) = P(Ti = 1 |

Xi ) The propensity score, e(X), is a type of balancing score such that the

treatment and covariates are conditionally independent given the score, T⊥

X | e(X) As a result, for a given propensity score, treatment assignment is

random The true propensity score in an observational study is unknown andmust be estimated Because of the large number of covariates required to sat-isfy the treatment ignorability assumption, the propensity score is typicallyestimated parametrically by regressing the covariates on treatment status andobtaining the estimated propensity score, e(X) Machine-learning methods

have been developed for prediction and have been applied to the tion of the propensity score (see References 12–15) Variables included in thepropensity score model consist of confounders and those related to the out-come but not to the treatment The latter are included to decrease the variance

estima-of the estimated treatment effect [16] Instrumental variables, those related totreatment but not to the outcome, should be excluded [17] The rationale forthe exclusion of instrumental variables under treatment ignorability relates

to the fact that their inclusion does not decrease the bias of the estimatedtreatment effect but does increase the variance Chapter 2 provides a detailedaccount of instrumental variables methodology

By their construction, propensity scores reduce the dimensionality of thecovariate space so that they can be utilized to match, stratify, or weightobservations These techniques are next described Inclusion of the propen-sity score as a predictor in a regression model of the outcome to replace theindividual covariates constitutes a simpler dimension reduction approachcompared to other estimators that use both the complete outcome regressionand treatment mechanism (see Section 1.3.3) However, if the distribution ofpropensity scores differs between treatment groups, there will not be bal-ance [18] between treated and control units when using e(X) as a covariate;

subsequent results may display substantial bias [19] Thus, methods that donot make use of the propensity score, such as G-computation (Section 1.3.2.2),

still benefit from an analysis of the propensity score, including testing forempirical violations of the positivity assumption.

1.3.1.1 Matching

Matching methods seek to find units with different levels of the treatmentbut having similar levels of the covariates Matching based on the propen-sity score facilitates the matching problem through dimension reduction.Several choices must be made that impact the degree of incomplete match-ing (inability to find a control unit to match to a treated unit) and inexactmatching (incomparability between treated and control units) These consid-erations include determination of the structure of the matches (one treatedmatched to one control, one-to-k, or one-to-variable), the method of findingmatches (greedy vs optimal matching), and the closeness of the matches (willany match do or should only close matches be acceptable) The literature onmatching is broad on these topics We refer the reader to Rassen et al [20]for discussion about matching structure, Gu and Rosenbaum [21] for a dis-cussion on the comparative performance of algorithms to find matches, andRosenbaum [22] for options for defining closeness of matches

Let j m (i) represent the index of the unit that is m th closest to unit i

among units with the opposite treatment to that of unit i, JM(i) the set of

indices for the first M matches for unit i, such that JM(i) = j1(i), , jM(i),

and K M(i) the number of times unit i is used as a match Lastly, define

K M(i) =N

l=1I i ∈ J M(l), where I is the indicator function Then the ATE

estimator and its corresponding variance are

Much of the preceding discussion assumed a larger pool of controls to findmatches for treated subjects—an estimator using this strategy provides infer-ence for the ATT Estimating the ATE additionally requires identification oftreatment matches for each control group unit Therefore, the entire match-ing process is repeated to identify matches for units in the control group

The matches found by both procedures are combined and used to computethe ATE.

1.3.1.2 Stratification

Stratification methods, also referred to as subclassification methods, dividesubjects into strata based on the estimated propensity score Within eachstratum, treatment assignment is assumed random As with matching, sub-classification can be accomplished without using the propensity score, butthis runs into problems of dimensionality Commonly, subjects are dividedinto groups by quintiles of the estimated propensity score, as Rosenbaumand Rubin [24] showed that using quintiles of the propensity score to strat-ify eliminates approximately 90% of the bias due to measured confounders

in estimating the absolute treatment effect parameter, = Y1− Y0 The age effect is estimated in each stratum as the average of the differences inoutcomes between the treated and control:

where N iq is the number of units in stratum q with treatment i, and I q

indicates membership in stratum q , so T ∩ I q would indicate that a subject

in stratum q received the treatment The overall average is computed by

averaging the within-strata estimates based on their sample sizes:

identi-1.3.1.3 Inverse Probability of Treatment Weighted (IPTW) Estimators

The intuition behind weighting is that units that are underrepresented in one

of the treatment groups are upweighted and units that are overrepresentedare downweighted The ATE can be estimated as

using the estimated propensity score, e(X) We denote this estimate HT-IPTW

to acknowledge the Horvitz–Thompson [26] ratio estimator utilized in vey sampling IPTW estimators solve an estimating equation that sets theestimating function to zero and aims to find an estimator that is a solution ofthe equation For example, consider

sur-N



i=1

D( ˆ)(Ti , Y i , X i ) = 0,

where D ()(T i , Y i , X i ) defines the estimating function and ˆ is an

estima-tor of the parameter that is a solution of the estimating equation Robins

et al [27] derived variance estimators, but bootstrapping can also be used.Inverse propensity score weighting is sensitive to outliers Treated subjectswith a propensity score close to one or control subjects with a propensityscore close to zero will result in large weights The weights can be trimmedbut doing so introduces bias in the estimation of the treatment effect [28].Robins et al [29] propose using stabilizing weights, such that

IPTW estimators are known to have problems with large variance estimates

in finite samples Inverse probability weights can be used to estimate meters defined by a marginal structural model, which we do not discuss here(see Reference 29) See References 30 and 31 for details regarding derivingvariances using the empirical sandwich method Alternatively, a bootstrapprocedure may be applied to the whole process, including estimation of thepropensity score

para-1.3.2 Methods Using the Outcome Regression

1.3.2.1 Multiple Regression Modeling

The ATE can be estimated by the treatment coefficient from regression of theoutcome on the treatment and all of the confounders The functional form

of the relationship between the outcome and covariates needs to be correctlyspecified The risk difference can be validly estimated by fitting an ordinaryleast squares regression model and using the robust variance to account fornonnormality of the error terms This approach is exactly equivalent to fitting

a generalized linear model for a binomial outcome with the identity link androbust variance

In the case of no overlap of the observed covariates between treatmentgroups, the model cannot be fit as the design matrix will be singular There-fore, erroneous causal inferences are prohibited by the mechanics of theestimation procedure in the case of complete nonoverlap However, stan-dardized differences should still be examined to see how the treated andcontrol groups differ, even under the assumption of no unmeasured con-founding If there is little overlap, causal inferences would be based onextrapolations, and hence, on less solid footing.

1.3.2.2 G-Computation

G-computation (G-computation algorithm formula, G-formula, computation) is completely nonparametric [32], but we focus on parametricG-computation, which is a maximum-likelihood-based substitution estima-tor [33] Substitution estimators involve using a maximum-likelihood-typeestimator (e.g., regression, super learning) for the outcome regression andplugging it into the parameter mapping that defines the feature we areinterested in estimating—here, that feature is the average treatment effectμ1− μ0 For further discussion and references, the reader can consult Chap-ter 3 Under ignorability of the treatment assignment, the G-computationformula permits identification of the distribution of potential outcomes based

Generalized-on the observed data distributiGeneralized-on In step 1, a regressiGeneralized-on model or otherconsistent estimator for the relationship of the outcome with treatment(and covariates) is obtained In step 2, (a) set each unit’s treatment indica-

tor to T= 1 and obtain predicted outcomes using the fit from step 1 and

(b) repeat step 2(a) by setting each unit’s treatment indicator to T = 0 Thetreatment effect is the difference between ˆY 1i and ˆY 0i for each unit, aver-aged across all subjects When there are no treatment covariate interactions,linear regression and G-computation that uses a parametric linear regres-sion provide the same answer for a continuous outcome We can definethis as

where ˆE (Y | T i = t, X i ) is the regression of Y on X in the treatment

group T = t Two points are worth noting First, if the outcome regression

is not estimated consistently, the G-computation estimator may be biased.Second, while positivity violations will not be obvious when implement-ing a G-computation estimator, they remain important to assess, and canlead to a nonidentifiable parameter or substantially biased and inefficientestimate

1.3.3 Methods Using the Treatment Assignment Mechanism

and the Outcome

Double robust methods use an estimator for both the outcome regressionand the treatment assignment Estimators in this class may be preferablebecause they are consistent for the causal parameters if either the outcomeregression or treatment assignment regression is consistently estimated [34].Two double robust methods include the augmented inverse probability oftreatment-weighted estimator (A-IPTW) and the targeted maximum likeli-hood estimator (TMLE)

1.3.3.1 Augmented Inverse Probability Weighted Estimators

Like IPTW estimators, A-IPTW estimators are also based on estimating

equa-tions but differ in that A-IPTW estimators are based on the efficient influence

curve An efficient influence curve is the derivative of the log-likelihood

func-tion with respect to the parameter of interest The efficient influence curve is

a function of the model and the parameter, and provides double robust mators with many of their desirable properties, including consistency andefficiency [35] The A-IPTW for the ATE is

where ˆE (Y | T i = t, X i ) is the regression of Y on X in the treatment group

T = t, and I () is an indicator function The nuisance parameters in the

esti-mating equation for the A-IPTW are the treatment assignment mechanismand the outcome regression Further discussion of estimating equations andefficient influence curve theory can be found in References 15, 35, and 36 Ofnote, A-IPTW estimators ignore the constraints imposed by the model by notbeing substitution estimators For example, an A-IPTW estimator for a binaryoutcome may produce predicted probabilities outside the range [0,1] Thus,finite sample efficiency may be impacted, even though asymptotic efficiencyoccurs if both the outcome regression and treatment assignment mechanismare consistently estimated

1.3.3.2 Targeted Maximum Likelihood Estimator

The TMLE has a distinct algorithm for estimation of the parameter of interest,sharing the double robustness properties of the A-IPTW estimator, but boast-ing additional statistical properties TMLE is a substitution estimator; thus,

unlike the A-IPTW, it does respect the global constraints of the model fore, among other advantages, this improves the finite sample performance

There-of the TMLE

The TMLE algorithm for the ATE involves two steps First, the

out-come regression E[Y | T, X] and the treatment assignment mechanism e(X)

are estimated Denote the initial estimate ˆE[Y | T, X] = Q0(T, X) and the

where  is estimated from the regression of Y on (T/(  e(X))) − ((1 − T)/ (1 −  e(X))) with an offset Q0(T, X) The estimator for the ATE is the given by

regres-1.4 Assessing Validity of Assumptions

In this section, we introduce ways to assess the assumptions outlined in tion 1.2.2 Methods for testing the assumptions given the data (or possiblyadditional data) are areas of active research and this section is not exhaus-tive SUTVA and ignorability of treatment assignment are untestable, butempirical data can provide evidence for how tenable these assumptions are

Sec-in practice In contrast, positivity and constant treatment effect are statisticalassumptions that can be directly tested with the data

1.4.1 SUTVA

As previously mentioned, SUTVA is composed of two parts: (1) no ence and (2) no variation in treatment SUTVA is generally argued heuris-tically, but recent research uses the data to assess the no interference por-tion, mainly in randomized studies Hudgens and Halloran [39] introducethe terminology of direct and indirect effects where the direct effect is an

interfer-individual’s response to treatment and the response to interference is theindirect effect Detecting indirect effects is a way to assess the first compo-

nent of SUTVA For the randomized setting, Aronow [40] presents a post

hoc method to detect interference using a conditional randomization test to

calculate the dependence between outcomes on the treatment of other units.However, for the second component, no variation in treatment refers tothe actual or levels of treatments or the precise treatment procedure, ratherthan the treatment effects We cannot assess this from the data alone in anypractical or feasible way When treatment is a drug intervention, one mightquestion whether the patient really took 10 mg or if they received anotherdose If we had millions of dollars and could collect unlimited variablesrelated to precisely how every procedure was performed, we could ensurethat there is no variation in the actual treatment For the radial versus femoralartery access example, perhaps we would measure how high the surgeon’shands were from the incision, the time in between sedation and the beginning

of procedure, number of hours the surgeon had slept, and so on

1.4.2 Ignorability

Ignorability of the treatment assignment is not directly testable and largelyassessed by subject matter knowledge Several strategies can bolster theviability of the assumption [41] however Multiple control or comparisongroups that differ with respect to an unmeasured confounder, if available,can be used If outcomes between the two control groups do not differ,then this observation would support the argument that the unmeasured con-founder is not responsible for any treatment–control outcome differences.Another option is to identify an outcome that is associated with an unmea-sured covariate but where a treatment would not expect to have any effect

Such outcomes, referred to as control outcomes, provide a means to detect

unobserved confounding Tchetgen [42] proposes a method to correct mates using control outcomes Finally, Rosenbaum [22] provides approaches

esti-to perform a sensitivity analysis for an unobserved confounder throughexamination of a range of potential correlations between the unobserved con-founder and the treatment assignment, and the unmeasured confounder andthe outcome

1.4.3 Positivity

Positivity or overlap can be measured through examination of the butions of covariates for the treated and control subjects While there aremany measures of balance, the difference in average covariates scaled by the

distri-sample standard deviation, d, provides an intuitive metric It is calculated as

d = ¯x1 j − ¯x0 j

(s2

1 j + s2

where¯x ij is the mean of covariate j among those with treatment i and s ijis the

estimated standard deviation The quantity d is interpreted as the number of

standard deviations the treated group is above the control group Mappingthe standardized differences to percentiles provides a mechanism to describethe extent of nonoverlap between two groups For instance, a standardizeddifference of 0.1 indicates 7.7% nonoverlap of the two normal distributions;

a standardized difference of 0 indicates complete overlap of the two groups;and a standardized difference of 0.7 corresponds to 43.0% nonoverlap Rules

of thumb suggest that a standardized difference less than 0.1 is ble [43] Examination of the standardized differences alone characterizes onlymarginal distributions—the distribution of individual covariates Becauseareas of weak overlap may exist, reviewing the distributions of the estimatedpropensity scores stratified by treatment groups is recommended

negligi-1.4.4 Constant Treatment Effect

The assumption of a constant treatment effect may be explored by ducing interactions between the treatment and subgroup indicators, or by

intro-dividing the population into subgroups based on X i, estimating an age causal effect within each subgroup, and comparing the constancy ofsubgroup-specific causal effects Cases in which the treatment effect may not

aver-be constant should aver-be identified a priori as well as the size of meaningful

treatment effect heterogeneity in order to avoid multiple testing

1.5 Radial versus Femoral Artery Access for PCI

We return to the PCI example introduced earlier to determine whether accessvia the radial artery reduces the risk of in-hospital complications compared

to access via the femoral artery Table 1.3 indicated imbalances between theradial and femoral artery-accessed subjects For instance, the standardizeddifference for use of thrombin is−0.6285, indicating 40% nonoverlap betweenthe distribution of thrombin use for those undergoing PCI via the radialartery and those via the femoral artery Ten of the observed covariates havestandardized differences greater than 0.1 or 7.7% nonoverlap

1.5.1 Estimating Treatment Assignment: Probability of Radial

Artery Access

The propensity score was estimated using logistic regression The set ofcovariates initially considered were determined by conversations with car-diologists who perform PCI A primary model specification was selected

to access via the femoral artery Table 1.3 indicated imbalances between theradial and femoral artery-accessed subjects For instance,... subgroup indicators, or by

intro-dividing the population into subgroups based on X i, estimating an age causal effect within each subgroup, and comparing the constancy... propensity score was estimated using logistic regression The set ofcovariates initially considered were determined by conversations with car-diologists who perform PCI A primary model specification