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Methods in
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Patrick S. Parfrey
Brendan J. Barrett Editors
Clinical
Epidemiology
Practice and Methods
Third Edition
METHODS IN MOLECULAR BIOLOGY
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Clinical Epidemiology
Practice and Methods
Third Edition
Edited by
Patrick S. Parfrey and Brendan J. Barrett

Clinical Epidemiology Unit, Faculty of Medicine, Memorial University of Newfoundland, St. John’s, NL,
Canada
Editors
Patrick S. Parfrey Brendan J. Barrett
Clinical Epidemiology Unit Clinical Epidemiology Unit
Faculty of Medicine Faculty of Medicine
Memorial University of Newfoundland Memorial University of Newfoundland
St. John’s, NL, Canada St. John’s, NL, Canada
ISSN 1064-3745 ISSN 1940-6029 (electronic)

Methods in Molecular Biology
ISBN 978-1-0716-1137-1 ISBN 978-1-0716-1138-8 (eBook)
https://doi.org/10.1007/978-1-0716-1138-8
© Springer Science+Business Media, LLC, part of Springer Nature 2021

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Preface
Clinical epidemiology provides the scientific basis for the practice of medicine, because it
focuses on the diagnosis, prognosis, and management of human disease. It is a relatively
recent science that initially focused on longitudinal studies, randomized controlled trials,
and evaluation of diagnostic tests, and progressed to evidence-based decision-making
revolving around critical appraisal, systematic reviews, meta-analysis, health technology
assessment, clinical practice guidelines, and health economics.
More recently, clinical epidemiology has extended to knowledge translation and patient
engagement together with endeavors to improve health-related behaviors using implemen-
tation science, and availing of administrative databases and big data technology.
Issues related to research design, measurement, and evaluation are critical to clinical
epidemiology. This third edition of Clinical Epidemiology: Practice and Methods has updated
chapters on longitudinal studies, randomized trials, other research methods, and evidence-
based decision-making, and includes a new section on changing health-related behaviors. Its
intended reach is consequently wide not only to include trainees in clinical epidemiology and
researchers who want to undertake clinical research, whether they be clinical practitioners or
basic scientists who want to extend their work to humans, but also users of clinical research
findings whether they be clinical practitioners or decision makers in the health system.
This book is divided into six parts. The first part is concerned with how to frame a
clinical research question and choose the appropriate design, biases that may occur in clinical
research, and the ethics associated with doing a research project in humans.
Parts II–IV discuss issues of design, measurement, and analysis that pertain to various
research questions, including determination of risk in longitudinal studies, assessment of
therapy in randomized controlled trials, and evaluation of diagnostic tests.
Part V presents methods in the various components of evidence-based decision-making
and Part VI is focused on interventions that could change health-related behaviors. In view
of the recent emphasis of granting agencies on knowledge translation and patient engage-
ment Chapters 25, 29, and 32 should be of interest.
The content varies from the basics of clinical epidemiology to more advanced chapters
examining bias (Chapter 3), the analysis of longitudinal studies (Chapters 7 and 8), rando-
mized trials (Chapters 16 and 17), and genetic epidemiology (Chapter 19). Examples and
case studies have been encouraged particularly in Part VI on Changing Health-Related
Behaviors.
All the contributors to this volume are practicing clinical epidemiologists, who hope the
reader will join them in doing research focused on improving clinical outcomes.
St. John’s, NL, Canada Patrick S. Parfrey

Brendan J. Barrett
v
Contents
Preface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . v
Contributors. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xi
1 On Framing the Research Question and Choosing the Appropriate

Research Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1
Patrick S. Parfrey and Pietro Ravani
2 Bias in Clinical Research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 17
Susan Stuckless and Patrick S. Parfrey
3 Definitions of Bias in Clinical Research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 35
Geoffrey Warden
4 Research Ethics for Clinical Researchers . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 53
John D. Harnett
5 Ethical, Legal, and Social Issues (ELSI) in Clinical Genetics Research . . . . . . . . . 65
Daryl Pullman and Holly Etchegary
6 Longitudinal Studies 1: Determinants of Risk . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 83
Sean W. Murphy
7 Longitudinal Studies 2: Modeling Data Using Multivariate Analysis. . . . . . . . . . . 103
Pietro Ravani, Brendan J. Barrett, and Patrick S. Parfrey
8 Longitudinal Studies 3: Data Modeling Using Standard Regression
Models and Extensions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 125
Pietro Ravani, Brendan J. Barrett, and Patrick S. Parfrey
9 Longitudinal Studies 4: Matching Strategies to Evaluate Risk . . . . . . . . . . . . . . . . 167
Matthew T. James
10 Longitudinal Studies 5: Development of Risk Prediction Models
for Patients with Chronic Disease . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 179
Navdeep Tangri and Claudio Rigatto
11 Randomized Controlled Trials 1: Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 193
Bryan M. Curtis, Brendan J. Barrett, and Patrick S. Parfrey
12 Randomized Controlled Trials 2: Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 213
Robert N. Foley and Patrick S. Parfrey
13 Randomized Controlled Trials 3: Measurement and Analysis
of Patient-Reported Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 229
Michelle M. Richardson and Klemens B. Meyer
14 Randomized Controlled Trials 4: Planning, Analysis,
and Interpretation of Quality-of-Life Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 247
Robert N. Foley and Patrick S. Parfrey
vii
viii Contents
15 Randomized Controlled Trials 5: Biomarkers and Surrogates/Outcomes . . . . . . 261

Claudio Rigatto and Brendan J. Barrett
16 Randomized Controlled Trials 6: Determining the Sample Size
and Power for Clinical Trials and Cohort Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . 281
Tom Greene
17 Randomized Controlled Trials 7: On Contamination
and Estimating the Actual Treatment Effect. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 307
Patrick S. Parfrey
18 Evaluation of Diagnostic Tests. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 319
Brendan J. Barrett and John M. Fardy
19 Genetic Epidemiology of Complex Phenotypes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 335
Darren D. O’Rielly and Proton Rahman
20 Qualitative Research in Clinical Epidemiology . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 369
Stephanie Thompson and Kara Schick-Makaroff
21 Evidence-Based Decision-Making 1: Critical Appraisal. . . . . . . . . . . . . . . . . . . . . . . 389
Laurie K. Twells
22 Evidence-Based Decision-Making 2: Systematic Reviews
and Meta-Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 405
Aminu Bello, Ben Vandermeer, Natasha Wiebe,
Amit X. Garg, and Marcello Tonelli
23 Evidence-Based Decision Making 3: Health Technology Assessment . . . . . . . . . . 429
Daria O’Reilly, Richard Audas, Kaitryn Campbell,
Meredith Vanstone, James M. Bowen, Lisa Schwartz,
Nazila Assasi, and Ron Goeree
24 Evidence-Based Decision Making 4: Clinical Practice Guidelines. . . . . . . . . . . . . . 455
Tae Won Yi, Sine Donnellan, and Adeera Levin
25 Evidence-Based Decision Making 5: Knowledge Translation
and the Knowledge to Action Cycle . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 467
Braden J. Manns
26 Evidence-Based Decision Making 6: Administrative Databases
as Secondary Data Source for Epidemiologic and Health
Service Research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 483
Tanvir Turin Chowdhury and Brenda R. Hemmelgarn
27 Evidence-Based Decision Making 7: Health Economics
in Clinical Research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 501
Braden J. Manns
28 Evidence-Based Decision-Making 8: A Primer on Health Policy
for Researchers . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 517
Victor Maddalena and Maisam Najafizada
29 Changing Health-Related Behaviors 1: Patient-Oriented Research
and Patient Engagement in Health Research . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 537
Catherine Street, Laurie K. Twells, Toni Leamon,
Lynn Taylor, and Holly Etchegary
Contents ix
30 Changing Health-Related Behaviors 2: On Improving the Value

of Health Spending . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 553
Karen Dickson, Robert Wilson, Owen Parfrey, and Patrick S. Parfrey
31 Changing Health-Related Behaviors 3: Lessons from Implementation
Science . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 571
Amanda Hall, Helen Richmond, Krista Mahoney, and James Matthews
32 Changing Health-Related Behaviors 4: Realizing Impact of Health
Research Through Knowledge Translation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 597
Kate Lambert, Krista Mahoney, and Patrick S. Parfrey
33 Changing Health-Related Behaviours 5: On Interventions to Change
Physician Behaviours . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 613
Cheryl Etchegary, Lynn Taylor, Krista Mahoney,
Owen Parfrey, and Amanda Hall
34 Changing Health-Related Behaviors 6: Analysis, Interpretation,
and Application of Big Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 631
Randy Giffen and Donald Bryant
Index . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 645
Contributors
NAZILA ASSASI • Program for Assessment of Technology in Health (PATH), St. Joseph’s
Healthcare Hamilton, Hamilton, ON, Canada; Department of Clinical Epidemiology
and Biostatistics, Faculty of Health Sciences, McMaster University, Hamilton, ON,
Canada
RICHARD AUDAS • Division of Community Health and Humanities, Faculty of Medicine,
Memorial University of Newfoundland, St. John’s, NL, Canada
BRENDAN J. BARRETT • Clinical Epidemiology Unit, Faculty of Medicine, Memorial
University of Newfoundland, St. John’s, NL, Canada
AMINU BELLO • Division of Nephrology, Department of Medicine, University of Alberta,
Edmonton, AB, Canada
JAMES M. BOWEN • Program for Assessment of Technology in Health (PATH), St. Joseph’s
Canada
DEONALD BRYANT • Quality of Care NL, Faculty of Medicine, Memorial University of
Newfoundland, St. John’s, NL, Canada
KAITRYN CAMPBELL • Program for Assessment of Technology in Health (PATH), St. Joseph’s
Canada
TANVIR TURIN CHOWDHURY • Department of Family Medicine, Cumming School of
Medicine, University of Calgary, Calgary, AB, Canada; Department of Community
Health Sciences, Cumming School of Medicine, University of Calgary, Calgary, AB,
Canada
BRYAN M. CURTIS • Department of Medicine (Nephrology), Faculty of Medicine, Memorial
KAREN DICKSON • Quality of Care NL, Department of Medicine, Memorial University,
St. John’s, NL, Canada
SINE DONNELLAN • Division of Nephrology, University of British Colombia, Vancouver, BC,
Canada
CHERYL ETCHEGARY • Quality of Care NL, Faculty of Medicine, Memorial University of
HOLLY ETCHEGARY • Strategy for Patient-Oriented Research (SPOR—CIHR), Faculty of
Medicine, Memorial University, St. John’s, NL, Canada
JOHN M. FARDY • Department of Medicine, Memorial University of Newfoundland,
St. John’s, NF, Canada
ROBERT N. FOLEY • USRDS Co-ordinating Center, University of Minnesota, Minneapolis,
MN, USA
AMIT X. GARG • Division of Nephrology, Department of Epidemiology and Biostatistics,
Western University, London, ON, Canada
RANDY GIFFEN • IBM Canada, Ottawa, ON, Canada
RON GOEREE • Program for Assessment of Technology in Health (PATH), St. Joseph’s
xi
xii Contributors

Canada
TOM GREENE • Internal Medicine, School of Medicine, University of Utah, Salt Lake City,
UT, USA
AMANDA HALL • Primary Healthcare Research Unit, Faculty of Medicine, Memorial
JOHN D. HARNETT • Faculty of Medicine, Health Science Centre, Memorial University, St.
John’s, NL, Canada
BRENDA R. HEMMELGARN • Department of Community Health Sciences, Cumming School of
Medicine, University of Calgary, Calgary, AB, Canada
MATTHEW T. JAMES • Departments of Medicine and Community Health Sciences, University
of Calgary, Calgary, AL, Canada
KATE LAMBERT • NL SUPPORT, Memorial University of Newfoundland, St. John’s, NL,
Canada
TONI LEAMON • NL SUPPORT Patient Advisory Council, Strategy for Patient-Oriented
Research (SPOR—CIHR), Memorial University of Newfoundland (Grenfell Campus), St.
John’s, NL, Canada
ADEERA LEVIN • Division of Nephrology, University of British Colombia, Vancouver, BC,
Canada
VICTOR MADDALENA • Faculty of Medicine, Division of Community Health and Humanities,
Memorial University, St. John’s, NL, Canada
KRISTA MAHONEY • Community Health & Humanities, Quality of Care NL, Memorial
BRADEN J. MANNS • Cumming School of Medicine, University of Calgary, Calgary, AB,
Canada
JAMES MATTHEWS • School of Public Health, Physiotherapy and Sports Science, University
College Dublin, Dublin, Ireland
KLEMENS B. MEYER • William B. Schwartz Division of Nephrology, Tufts Medical Center,
Boston, MA, USA; Outcomes Monitoring Program, Dialysis Clinic, Inc., Boston, MA, USA
SEAN W. MURPHY • Department of Medicine (Nephrology), Memorial University of
MAISAM NAJAFIZADA • Faculty of Medicine, Division of Community Health and Humanities,
DARIA O’REILLY • Program for Assessment of Technology in Health (PATH), St. Joseph’s
Canada
DARREN D. O’RIELLY • Molecular Genetics Laboratory, Eastern Health, Faculty of Medicine,
Memorial University of Newfoundland, St. John’s, NL, Canada
OWEN PARFREY • Quality of Care NL, Faculty of Medicine, Memorial University of
PATRICK S. PARFREY • Quality of Care NL, Faculty of Medicine, Memorial University of
DARYL PULLMAN • Division of Community Health and Humanities, Faculty of Medicine,
PROTON RAHMAN • Department of Medicine (Rheumatology), Memorial University of
Contributors xiii
PIETRO RAVANI • Division of Nephrology, Department of Medicine, University of Calgary,

Calgary, AB, Canada
MICHELLE M. RICHARDSON • William B. Schwartz Division of Nephrology, Tufts Medical
Center, Boston, MA, USA; Outcomes Monitoring Program, Dialysis Clinic, Inc., Boston,
MA, USA
HELEN RICHMOND • Primary Healthcare Research Unit, Faculty of Medicine, Memorial
CLAUDIO RIGATTO • Department of Medicine, Seven Oaks General Hospital, University of
Manitoba, Winnipeg, MB, Canada
KEARA SCHICK-MAKAROFF • Faculty of Nursing, University of Alberta, Edmonton, AB,
Canada
LISA SCHWARTZ • Department of Clinical Epidemiology and Biostatistics, Faculty of Health
Sciences, McMaster University, Hamilton, ON, Canada; Centre for Health Economics and
Policy Analysis (CHEPA), McMaster University, Hamilton, ON, Canada
CATHERINE STREET • NL SUPPORT, Strategy for Patient-Oriented Research (SPOR—
CIHR), Faculty of Medicine, Memorial University of Newfoundland, St. John’s, NL,
Canada
SUSAN STUCKLESS • Quality of Care NL, Faculty of Medicine, Memorial University of
NAVDEEP TANGRI • Department of Medicine, Seven Oaks General Hospital, University of
Manitoba, Winnipeg, MB, Canada
LYNN TAYLOR • Quality of Care NL, Faculty of Medicine, Memorial University of
STEPHANIE THOMPSON • Department of Medicine, University of Alberta, Edmonton, AB,
Canada
MARCELLO TONELLI • Department of Medicine, University of Calgary, Calgary, AB,
Canada
LAURIE K. TWELLS • School of Pharmacy and Faculty of Medicine, NL SUPPORT, Strategy
for Patient-Oriented Research (SPOR—CIHR), Memorial University of Newfoundland,
BEN VANDERMEER • Department of Pediatrics, University of Alberta, Edmonton, AB,
Canada
MEREDITH VANSTONE • Department of Clinical Epidemiology and Biostatistics, Faculty of
Health Sciences, McMaster University, Hamilton, ON, Canada; Centre for Health
Economics and Policy Analysis (CHEPA), McMaster University, Hamilton, ON, Canada
GEOFFREY WARDEN • Faculty of Medicine, Memorial University of Newfoundland, St. John’s,
NL, Canada
NATASHA WIEBE • Faculty of Medicine and Dentistry, University of Alberta, Edmonton, AB,
Canada
ROBERT WILSON • Quality of Care NL, Department of Medicine, Memorial University,
TAE WON YI • Division of Nephrology, University of British Colombia, Vancouver, BC,
Canada
Chapter 1
On Framing the Research Question and Choosing

the Appropriate Research Design
Patrick S. Parfrey and Pietro Ravani
Abstract
Clinical epidemiology is the science of human disease investigation with a focus on diagnosis, prognosis,
and treatment. The generation of a reasonable question requires definition of patients, interventions,
controls, and outcomes. The goal of research design is to minimize error, ensure adequate samples, measure
input and output variables appropriately, consider external and internal validities, limit bias, and address
clinical as well as statistical relevance. The hierarchy of evidence for clinical decision-making places rando-
mized controlled trials (RCT) or systematic review of good-quality RCTs at the top of the evidence
pyramid. Prognostic and etiologic questions are best addressed with longitudinal cohort studies.
Key words Clinical epidemiology, Methodology, Research design, Evidence-based medicine, Rando-
mized controlled trials, Longitudinal studies
1 Introduction
Clinical epidemiology is the science of human disease investigation,

with a focus on problems of most interest to patients: diagnosis,
prognosis, and management.
In this chapter, we consider how to frame the research ques-
tion, define error, measurement, sampling, validity, the choice of
research design, and the difference between clinical relevance and
statistical significance. In addition, here, we provide an overview of
principles and concepts that are discussed in more details in
subsequent chapters.
2 Framing the Clinical Research Question
The research process usually starts with a general idea or initial

problem.
Research ideas may originate from practical clinical problems,
request for proposals by funding agencies or private companies,
Patrick S. Parfrey and Brendan J. Barrett (eds.), Clinical Epidemiology: Practice and Methods, Methods in Molecular Biology,
vol. 2249, https://doi.org/10.1007/978-1-0716-1138-8_1, © Springer Science+Business Media, LLC, part of Springer Nature 2021
1
2 Patrick S. Parfrey and Pietro Ravani
reading the literature and thinking of ways to extend or refine

previous research, or the translation of basic science discoveries to
the clinic or the community. Literature review is always required to
identify related research, define the knowledge gap, avoid redun-
dancy when the answer is already clear, and set the research within a
proper conceptual and theoretical context based on what is already
known.
The next step is to generate a researchable question from the
general idea. This stage of conceptualization should generate test-
able hypotheses and delineate the exposure—outcome relationship
to be studied in a defined patient population, whether it be a study
of prognosis, diagnosis, or treatment. Thus, operationalization of
the proposed study requires characterization of the specific disease
to be studied, establishment of the input variable or exposure (test,
risk factor, or intervention) to be associated with an output or
clinical outcome. The latter may be the gold standard in a diagnos-
tic test, the clinical event in a cohort study evaluating risk, or the
primary clinical outcome in a randomized trial of an intervention.
Thus, the broad initial idea is translated into a feasible research
project. Narrowing down the area of research is necessary to for-
mulate an answerable question, in which the target population of
the study is determined along with a meaningful measure of
effect—the prespecified study outcome. This measure should sum-
marize how this outcome changes as the exposure or intervention
changes.
In framing researchable questions, it is crucial to define the
patients, interventions, controls, and outcomes (PICO) of rele-
vance. The study question should define the patients (P) to be
studied (e.g., prevalent or incident) through clearly defined eligi-
bility criteria. These criteria should specify the problem, the comor-
bid conditions to include (because the answer(s) to the research
question may vary by the condition, e.g., diabetes, cardiovascular
diseases); and those not to include (because for them the question
may be of less interest or hardly answerable, e.g., those with short
expected survival). Second, the type of exposure (intervention
(I) or prognostic factor or test) is defined, and its specifics (e.g.,
what does the intervention actually comprise). Next, the compari-
son group (C) is defined. Finally, the outcome of interest (O) is
declared.
Following consideration of the PICO issues, the researchable
question can then be posed, for example, “Does a particular statin
prevent cardiac events, when compared to conventional therapy, in
diabetic patients with stage 3 and 4 chronic kidney disease?”
The operationalization of the study must be consistent with its
purpose. If the question is one of efficacy (Does it work in the ideal
world?), then the measurement tools identified should be very
accurate, may be complex and expensive, and not necessarily useful
in practice. Opposite considerations are involved in effectiveness
On Framing the Research Question and Choosing the Appropriate Research Design 3
studies (Does it work in the real world?), and trade-offs between

rigor and practicality are necessary. Further operational steps in
clinical research involve limiting error, whether it be random or
systematic error, identifying a representative sample to study, deter-
mining a clinically relevant effect to assess, ensuring that the study is
feasible, cost-effective, and ethical.
3 Error
The goal of clinical research is to estimate population characteristics

(parameters) such as risks by making measurements on samples
from the target population. The hope is that the study estimates
be as close as possible to the true values in the population (accuracy)
with little uncertainty (imprecision) around them (Table 1). How-
ever, an error component exists in any study. This is the difference
between the value observed in the sample and the true value of the
phenomenon of interest in the parent population.
Table 1
Precision and accuracy in clinical studies
Precision Accuracy
Definition Degree to which a variable has nearly the same Degree to which a variable actually
value when measured several times represents what is supposed to
represent
Synonyms Fineness of a single measurement Closeness of a measurement or
Consistency—agreement of repeated estimate to the true value
measurements (reliability) or repeated Validity—agreement between
sampling data (reproducibility) measured and true values
Value to the Increase Power to detect effects Increase validity of conclusions
study
Threat Random error (variance) Systematic error (bias)
Maximization: Increase sample size Randomization
sampling
Maximization: Variance reduction Bias prevention/control
measurement
Observer sources Procedure standardization, staff training Blinding
Tool sources Calibration; automatization Appropriate instrument
Subject sources Procedure standardization, repetition & Blinding
averaging key measurements
Assessment Repeated measures (test/retest, inter/intra Comparison with a reference
observer: correlation, agreement, consistency) standard (gold standard; formal
experiments, RCT)
RCT randomized controlled trial
Fig. 1 The effect of the error type on study results. Each panel compares the distribution of a parameter
observed in a study (continuous lines) and the corresponding true distribution (dashed lines). Random error
lowers the precision of the estimates increasing the dispersion of the observed values around the average
(studies #3 and #4). Systematic error (bias) causes incorrect estimates or “deviations from the truth”: the
estimated averages correspond to rings distant from the target center (studies #1 and #3) even if results are
precise (study #1)
With permission Ravani et al., Nephrol Dial Transpl (19)
There are two main types of error: random or accidental error,

and systematic error (bias). Random errors are due to chance and
compensate since their average effect is zero. Systematic errors are
non-compensating distortions in measurement (Fig. 1). Mistakes
caused by carelessness, or human fallibility (e.g., incorrect use of an
instrument, error in recording or in calculations), may contribute
to both random and systematic errors. Both errors arise from many
sources, and both can be minimized using different strategies.
However, their control can be costly and complete elimination
may be impossible. Systematic error, as opposed to random error,
is not limited by increasing the study size and replicates if the study
is repeated.
Confounding is a special error since it is due to chance in
experimental designs, but it is a bias in nonexperimental studies.
Confounding occurs when the effect of the exposure is mixed with
that of another variable (confounder) related to both exposure and
outcome, which does not lie in the causal pathway between them.
For example, if high serum phosphate levels are found to be asso-
ciated with higher mortality, it is important to consider the con-
founding effect of low glomerular filtration rate in the assessment
of the relationship between serum phosphate and death [1].
For any given study, the design should aim to limit error. In
some cases, pilot studies are helpful in identifying the main poten-
tial sources of error (known sources of variability and bias—
Table 1) such that the design of the main study can control them
[2, 3]. Some errors are specific to some designs and will be dis-
cussed in a subsequent paper of this series. Both random and
systematic errors can occur during all stages of a study, from con-
ceptualization of the idea to sampling (participant selection) and
actual measurements (information collection).
4 Sampling
Once the target population has been defined, the next challenge is
to recruit study participants representative of the target population.
The sampling process is important, as usually a small fraction of the
target population is studied for reasons of cost and feasibility. Errors
in the sampling process can affect both the actual estimate and its
precision (Table 1, Fig. 2). To reduce sampling errors, researchers
must set up a proper sampling system and estimate an adequate
sample size.
Recruitment of a random sample of the target population is
necessary to ensure generalizability of study results. For example, if
we wish to estimate the prevalence of chronic kidney disease (CKD)
in the general population, the best approach would be to use
Fig. 2 Sampling bias. An unbiased sample is representative of and has the same
characteristics as the population from which it has been drawn. A biased sample
is not representative of the target population because its characteristics have
different distribution compared to the original population
random sampling, possibly over-sampling some subgroup of par-

ticular interest (e.g., members of a racial group) in order to have
sufficiently precise estimates for that subgroup [4, 5]. In this
instance, a sample of subjects drawn from a nephrology or a diabetic
clinic, any hospital department, school, workplace, or people walk-
ing down the street would not be representative of the general
population. The likelihood of CKD may be positively or negatively
related to factors associated with receiving care or working in a
particular setting. On the other hand, if a study aimed at under-
standing the characteristics of patients with CKD referred to a
nephrologist, a study of consecutive patients referred for CKD
would probably provide a reasonably generalizable result.
If the purpose of the study is to estimate a measure of effect due
to some intervention, then the sampling problem is not finished.
Here, the comparability of study groups, other than with regard to
the exposure of interest, must be ensured. Indeed, to measure the
effect of a therapy, we need to contrast the experience of people
given the therapy to those not so treated. However, people differ
from one another in myriad of ways, some of which might affect the
outcome of interest. To avoid such concerns in studies of therapy,
random assignment of study participants to therapy is recom-
mended to ensure comparability of study groups in the long run.
These must be of sufficient size to reduce the possibility that some
measurable or unmeasurable prognostic factors be associated with
one or other of the groups (random confounding).
The randomization process consists of three interrelated man-
euvers: the generation of random allocation sequences; strategies to
promote allocation concealment; and intention-to-treat analysis.
Random sequences are usually generated by means of computer
programs. The use of calendar or treatment days, birth dates, etc.,
is not appropriate since it does not guarantee unpredictability.
Allocation concealment is meant to prevent those recruiting trial
subjects from the knowledge of upcoming assignment and protect
selection biases. Useful ways to implement concealed allocation
include the use of central randomization or the use of sequentially
numbered sealed opaque envelopes. Intention-to-treat analysis
consists in keeping all randomized patients in their original assigned
groups during analysis regardless of adherence or any protocol
deviations. This is necessary to maintain group comparability.
5 Sample Size Estimation
When planning a comparative study, two possible random errors

(called type I and II errors) are considered. A type I error is made if
the results of a study have a statistically significant result when in
fact there is no difference between study groups. This risk of false
negative results is commonly set at 5% (equivalent to a significant
P value of 0.05). A Type II error is made if the results of a study are

nonsignificant when in fact a difference truly exists. This risk of
false-positive results is usually set at 10 or 20%. The other factors
that determine how large a study should be are the size of the effect
to be detected and the expected outcome variability. Different
methods (from closed formulae to simulation procedures) exist to
estimate the sample size depending on the type of response variable
and the analytical tool used to assess the input–output relationship
[6]. In all studies, the sample size will depend on the expected
variability in the data, effect size (delta), level of significance
(alpha error), and study power (1 beta error).
6 Measurement
6.1 Variable Types As in all sciences, measurement is a central feature of clinical epide-
miology. Both input and output variables are measured on the
sample according to the chosen definitions. Inputs can be measured
once at baseline if their value is fixed (e.g., gender), or more than
once if their value can change during the study (such as blood
pressure or type of therapy). Outputs can also be measured once
(e.g., average blood pressure values after 6 months of treatment) or
multiple times (repeated measures of continuous variables such as
blood pressure or events such as hospital admissions). The infor-
mation gained from input and output variables depends on the type
of observed data, whether it be qualitative nominal (unordered
categories, qualitative ordinal (ordered categories), quantitative
interval (no meaningful zero), or quantitative ratio (zero is
meaningful).
In clinical epidemiology, the type of outcomes influences study
design and determines the analytical tool to be used to study the
relationship of interest.
Intermediate variables are often considered surrogate outcome
candidates and used as an outcome instead of the final end-point to
reduce the sample size and the study cost (Table 2). Candidate
surrogate outcomes are many and include measures of the
underlying pathological process (e.g., vascular calcification) or of
preclinical disease (e.g., left ventricular hypertrophy). However,
well-validated surrogate variables highly predictive of adverse clini-
cal events, such as systolic blood pressure and LDL cholesterol, are
very few and only occasionally persuasive (Fig. 3). Furthermore,
although these surrogates may be useful in studies of the general
population, their relationship with clinical outcomes is not linear in
some conditions making them less useful in those settings
[7, 8]. Desired characteristics of a surrogate outcome are outlined
in Table 3. Hard outcomes that are clinically important and easy to
define are used to measure disease occurrence, as well as to estimate
the effects of an exposure.
Table 2
Comparison between final outcome and intermediate (surrogate) response
Surrogate marker Hard end point

Definition Relatively easily measured variables which The real efficacy measure of a clinical study
predict a rare or distant outcome
Use May substitute for the clinical endpoint; Response variable of a clinical study
provide insight into the causal pathway (outcome)
Example Brain natriuretic peptide; left ventricular Death (from all and specific causes);
hypertrophy cardiovascular or other specified events
Advantages (1) Reduction of sample size and duration A change in the final outcome answers the
(cost) of RCT; (2) assessment of essential questions on the clinical impact
treatments in situations where the use of of treatment
primary outcomes would be excessively
invasive or premature
Disadvantages (1) A change in valid surrogate end point (1) Large sample size and long duration
does not answer the essential questions (cost) of RCT; (2) assessment of
on the clinical impact of treatment treatments may be premature or invasive
(2) It may lack some of the desired
characteristics a primary outcome should
have
Fig. 3 Validity issues for a surrogate end point to be tested in a RCT

Surrogate marker validity: Is the plausible relationship between exposure (E) and the final hard outcome
(H) fully explained by the surrogate marker (S)?
6.2 Measurement Some systematic and random errors may occur during measure-
Errors ment (Table 1). Of interest to clinical trials are the strategies to
reduce performance bias (additional therapeutic interventions pref-
erentially provided to one of the groups) and to limit information
and detection bias (ascertainment or measurement bias) by mask-
ing (blinding) [9]. Masking is a process whereby people are kept
unaware of which interventions have been used throughout the
study, including when outcome is being assessed. Patient/clinician
blinding is not always practical or feasible, such as in trials compar-
ing surgery with non-surgery diets and lifestyles.
Finally, measurement error can occur in the statistical analysis
of the data. Important elements to specify in the protocol include
Table 3
Desired characteristics of a surrogate outcome
(1) Validity/reliability
(2) Availability, affordability; suitable for monitoring
(3) Dose–response relation predictive of the hard end point
(4) Existence of a cutoff point for normality
(5) High sensitivity, specificity, predictive values
(6) Changes rapidly/accurately in response to treatment
(7) Levels normalize in states of remission
definition of the primary and secondary outcome measures; how

missing data will be handled (depending on the nature of the data,
there are different techniques); subgroup (secondary) analyses of
interest; consideration of multiple comparisons and the inflation of
the type I error rate as the number of tests increases; the potential
confounders to control for; and the possible effect modifiers (inter-
action). This issue has implication for modeling techniques and will
be discussed in subsequent papers.
7 External and Internal Validity
The operational criteria applied in the design influence the external

and internal validity of the study (Fig. 4). Both construct validity
and external validity relate to generalization. However, construct
validity involves generalizing from the study to the underlying
concept of the study. It reflects how well the variables in the study
(and their relationships) represent the phenomena of interest. For
example, how well does the level of proteinuria represent the pres-
ence of kidney disease? Construct validity becomes important when
a complex process, such as care for chronic kidney disease, is being
described. Maintaining consistency between the idea or concept of
a certain care program and the operational details of its specific
components in the study may be challenging.
External validity involves generalizing conclusions from the
study context to other people, places, or times. External validity is
reduced if study eligibility criteria are strict, or the exposure or
intervention is hard to reproduce in practice. The closer the
intended sample is to the target population, the more relevant the
study is to this wider, but defined, group of people, and the greater
is its external validity. The same applies to the chosen intervention,
control, and outcome including the study context. The internal
validity of a study depends primarily on the degree to which bias is
Fig. 4 Structure of study design. The left panel represent the design phase of a study, when patient,
intervention, control, and outcome (PICO) are defined (conceptualization and operationalization). The right
panel corresponds to the implementation phase. Different types of bias can occur during sampling, data
collection, and measurement. The extent to which the results in the study can be considered true and
generalizable depend on its internal and external validity
minimized. Selection, measurement, and confounding biases can

all affect the internal validity.
In any study, there is always a balance between external and
internal validity, as it is difficult and costly to maximize both.
Designs that have strict inclusion and exclusion criteria tend to
maximize internal validity, while compromising external validity.
Internal validity is especially important in efficacy trials to under-
stand the maximum likely benefit that might be achieved with an
intervention, whereas external validity becomes more important in
effectiveness studies. Involvement of multiple sites is an important
way to enhance both internal validity (faster recruitment, quality
control and standardized procedures for data collection, manage-
ment, and analysis) and external validity (generalizability is
enhanced because the study involves patients from several regions).
8 Clinical Relevance vs. Statistical Significance
The concepts of clinical relevance and statistical significance are

often confused. Clinical relevance refers to the amount of benefit
or harm apparently resulting from an exposure or intervention that
is sufficient to change clinical practice or health policy. In planning
study sample size, the researcher has to determine the minimum
level of effect that would have clinical relevance. The level of
statistical significance chosen is the probability that the observed
results are due to chance alone. This will correspond to the proba-
bility of making a type I error, that is, claiming an effect when in fact
there is none. By convention, this probability is usually 0.05 (but
can be as low as 0.01). The P value or the limits of the appropriate
confidence interval (a 95% interval is equivalent to a significance
level of 0.05 for example) is examined to see if the results of the
study might be explained by chance. If P < 0.05, the null hypothe-
sis of no effect is rejected in favor of the study hypothesis, despite it
is still being possible that the observed results are simply due to
chance. However, since statistical significance depends on both the
magnitude of effect and the sample size, trials with very large
sample sizes theoretically can detect statistically significant but
very small effects that are of no clinical relevance.
9 Hierarchy of Evidence
Fundamental to evidence-based healthcare is the concept of “hier-

archy of evidence” deriving from different study designs addressing
a given research question (Fig. 5). Evidence grading is based on the
idea that different designs vary in their susceptibility to bias and,
therefore, in their ability to predict the true effectiveness of health-
care practices. For assessment of interventions, randomized con-
trolled trials (RCTs) or systematic review of good-quality RCTs are
at the top of the evidence pyramid, followed by longitudinal
cohort, case-control, cross-sectional studies, and case series at the
bottom [10]. However, the choice of the study design depends on
the question at hand and the frequency of the disease. Intervention
questions ideally are addressed with experiments (RCTs) since
observational data are prone to unpredictable bias and confounding
that only the randomization process will control. Appropriately
designed RCTs allow also stronger causal inference for disease
mechanisms.
Prognostic and etiologic questions are best addressed with
longitudinal cohort studies in which exposure is measured first and
participants are followed forward in time. At least two (and possibly
more) waves of measurements over time are undertaken. Initial
assessment of an input–output relationship may derive from case–
Fig. 5 Examples of study designs. In cross-sectional studies, inputs and outputs are measured simultaneously,
and their relationship is assessed at a particular point in time. In case–control studies, participants are
identified based on presence or absence of the disease and the temporal direction of the inquiry is reversed
(retrospective). Temporal sequences are better assessed in longitudinal cohort studies where exposure levels
are measured first and participants are followed forward in time. The same occurs in randomized controlled
trials (RCTs) where the assignment of the exposure is under the control of the researcher
P: probability (or risk)
control studies where the direction of the study is reversed. Partici-

pants are identified by the presence or absence of disease, and
exposure is assessed retrospectively. Cross-sectional studies may be
appropriate for an initial evaluation of the accuracy of new diagnos-
tic tests compared to a gold standard. Further assessments of diag-
nostic programs are performed with longitudinal studies
(observational and experimental). Common biases afflicting both
experimental and observational designs are discussed in Chapter 2
and defined in more detail in Chapter 3.
10 Experimental Designs for Intervention Questions
The RCT design is appropriate for assessment of the clinical effects

of drugs, procedures, or care processes, definition of target levels in
risk factor modification (e.g., blood pressure, lipid levels, and pro-
teinuria), and assessment of the impact of screening programs.
Comparison to a placebo may be appropriate if no current standard
therapy exists. When accepted therapies exist (e.g., statins as lipid
lowering agents, ACE-I for chronic kidney disease progression,
etc.), then the comparison group is an “active” control group that
receives usual or recommended therapy.
The most common type of RCT is the two group parallel-arm
trial (Fig. 5). However, trials can compare any number of groups.
In factorial trials, at least two active therapies (A; B) and their
combination (AB) are compared to a control (C). Factorial designs
can be efficient since more therapies are simultaneously tested in the
same study. However, the efficiency and the appropriate sample size
are affected by the impact of multiple testing on both type I and
type II errors, and whether there is an interaction between the
effects of the therapies. In absence of interaction, the effect of A,
for example, can be determined by comparing A + AB to B + C (and
the effect of B by comparing AB+B to C + A). Interactions where
use of A enhances the effectiveness of B, for example, do not reduce
the power of the study. However, if there is antagonism between
treatments, the sample size can be inadequate.
The crossover design is an alternative solution when the outcome
is reversible [11]. In this design, each participant serves as their own
control by receiving each treatment in a randomly specified
sequence. A washout period is used between treatments to prevent
carryover of the effect of the first treatment to the subsequent
periods. The design is efficient in that treatments are compared
within individuals, reducing the variation due to subject differ-
ences. However, limitations include possible differential carryover
(one of the treatments tends to have a longer effect once stopped);
period effects (different response of disease to early versus later
therapy); and a greater impact of missing data because they com-
promise within subject comparison and therefore variance
reduction.
Finally, RCTs may attempt to show that one treatment is not
inferior (under a one-sided hypothesis) or equivalent (under a
two-sided hypothesis) rather than superior to a comparable inter-
vention. In non-inferiority trials, the null hypothesis of inferiority is
rejected if the effect of an intervention lies within a certain pre-
specified non-inferiority margin. In equivalence trials, the null
hypothesis of nonequivalence is rejected if the effect of an interven-
tion lies within two prespecified margins. These studies are often
done when new agents are being added to a class (e.g., another
ACE inhibitor) or when a new therapy is already known to be

cheaper or safer than an existing standard. In such RCTs, the
study size is estimated based on a prespecified maximum difference
that would still be considered irrelevant. For example, the claim
might be made that a new ACE inhibitor is non-inferior to Enala-
pril, if the mean 24-h blood pressure difference between them was
no more than 3 mmHg. Non-inferiority trials have been criticized
as imperfections in study execution, which tend to prevent detec-
tion of a difference between treatments, actually work in favor of a
conclusion of non-inferiority. Thus, in distinction to the usual
superiority trial, poorly done studies may lead to the desired out-
come for the study sponsor.
11 Designs for Diagnostic Questions
When assessing a diagnostic test, the reference or “gold standard”

tests for the suspected target disorders are often either inaccessible
to clinicians or avoided for reasons of cost or risk. Therefore, the
relationship between more easily measured phenomena (patient
history, physical and instrumental examination, and levels of con-
stituents of body fluids and tissues) and the final diagnosis is an
important subject of clinical research. Unfortunately, even the most
promising diagnostic tests are never completely accurate.
Clinical implications of test results should ideally be assessed in
four types of diagnostic studies. Table 4 shows examples from
diagnostic studies of troponins in coronary syndromes. As a first
step, one might compare test results among those known to have
established disease to results from those free of disease. Cross-
sectional studies can address this question (Fig. 5). However,
since the direction of interpretation is from diagnosis back to the
test, the results do not assess test performance. Examining test
performance requires data on whether those with positive test
results are more likely to have the disease than those with normal
results [12]. When the test variable is not binary (i.e., when it can
assume more than two values), it is possible to assess the trade-off
between sensitivity and specificity at different test result cut-off
points [13]. In these studies, it is crucial to ensure independent
blind assessment of results of the test being assessed and the gold
standard to which it is compared, without the completion of either
being contingent on results of the other.
Longitudinal studies are required to assess diagnostic tests
aimed at predicting future prognosis or development of established
disease [12]. The most stringent evaluation of a diagnostic test is to
determine whether those tested have more rapid and accurate
diagnosis, and as a result better health outcomes, than those not
tested. The RCT design is the proper tool to answer this type of
question [14].
Table 4
Level of evidence in diagnostic studies using troponin as test (T) and acute myocardial infarction
(AMI) as target disorder (D)
Diagnostic question Direction Design Problems Example Reference

+
Do D patients have From D Cross- Reverse Difference in
different levels of T? back sectional association troponin levels by
to T Sampling AMI
bias
Are patients T+ more likely From T Cross- Effectiveness Troponin [12]
to be D+? to D sectional not performance in
assessed distinguishing AMI
Sampling
bias
Does the level of T predict From T Longitudinal Missing data Outcome study in [12]
D+/ ? to D Sampling subject at risk for
bias AMI
Do tested patients have From T Experiment Missing data Outcome [14]
better final outcomes to D (randomized)
than similar patients who comparison in
do not? subject at risk for
AMI
Positive (+); Negative ( ). Missing data are possible in longitudinal or experimental designs: for example, subjects lost
before assessment or with data not interpretable. Strategies should be set up to (1) minimize the likelihood of missing
information and (2) plan how subjects with missing information can be treated avoiding their exclusion (e.g., sensitivity
analysis, propensity analysis, etc.)
12 Maximizing the Validity of Nonexperimental Studies
When randomization is not feasible, the knowledge of the most

important sources of bias is important to increase the validity of any
study. This may happen for a variety of reasons: when study parti-
cipants cannot be assigned to intervention groups by chance either
for ethical reasons (e.g., in a study of smoking) or participant
willingness (e.g., comparing hemo- to peritoneal dialysis); the
exposure is fixed (e.g., gender); or the disease is rare and partici-
pants cannot be enrolled in a timely manner. When strategies are in
place to prevent bias, nonexperimental studies may yield similar
results to rigorous RCTs.
13 Reporting
Adequate reporting is critical to the proper interpretation and

evaluation of any study results. Guidelines for reporting primary
and secondary studies are in place to help both investigators and
consumers of clinical research [15]. Scientific reports may not fully
reflect how the investigators conducted their studies, but the qual-
ity of the scientific report is a reasonable marker for how the overall
project was conducted. The interested reader is referred to the
above referenced citations for more details of what to look for in
reports from prognostic, diagnostic, and intervention studies.
References
1. Chertow GM, Moe SM (2005) Calcification or markers in clinical studies: problems solved or
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(1997) Comparison of methods to predict bias in randomized controlled trials: impor-
equilibrated Kt/V in the HEMO Pilot Study. tance of allocation concealment and masking.
Kidney Int 52:1395–1405 Fam Med 39:132–137. http://www.cebm.
3. Wright JT Jr, Kusek JW, Toto RD et al (1996) net/levels_of_evidence.asp, last accessed
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pants in the African American Study of Kidney 10. Sibbald B, Roberts C (1998) Understanding
Disease and Hypertension (AASK) Pilot Study. controlled trials: crossover trials. BMJ
Control Clin Trials 17:3S–16S 316:1719
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(2006) Study design and participation rates of Evaluation of a rapid bedside assay for detec-
the New York City Health and Nutrition tion of serum cardiac troponin T. JAMA
Examination Survey. Prev Chronic Dis 3:A94 273:1279–1282
5. Robbins JM, Vaccarino V, Zhang H, Kasl SV 12. Sackett DL, Haynes RB, Guyatt GH, Tugwell
(2000) Excess type 2 diabetes in African- P (1991) The Interpretation of diagnostic data.
American women and men aged 40–74 and In: Sackett DL, Haynes RB, Guyatt GH, Tug-
socioeconomic status: evidence from the well P (eds) Clinical epidemiology, a basic sci-
Third National Health and Nutrition Examina- ence for clinical medicine. Little, Brown and
tion Survey. J Epidemiol Community Health Company, Toronto, CA, pp 117–119
54:839–845 13. Alp NJ, Bell JA, Shahi M (2001) A rapid
6. Julious SA (2004) Sample sizes for clinical trials troponin-I-based protocol for assessing acute
with normal data. Stat Med 23:1921–1986 chest pain. Q J Med 94:687–694. www.equa
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Chapter 2
Bias in Clinical Research

Susan Stuckless and Patrick S. Parfrey
Abstract
Clinical epidemiological research entails assessing the burden and etiology of disease, the diagnosis and
prognosis of disease, the efficacy of preventive measures or treatments, the analysis of the risks and benefits
of diagnostic and therapeutic maneuvers, and the evaluation of health care services. In all areas, the main
focus is to describe the relationship between exposure and outcome and to determine one of the following:
prevalence, incidence, cause, prognosis, or effect of treatment. The accuracy of these conclusions is
determined by the validity of the study. Validity is determined by addressing potential biases and possible
confounders that may be responsible for the observed association. Therefore, it is important to understand
the types of bias that exist and also to be able to assess their impact on the magnitude and direction of the
observed effect. The following chapter reviews the epidemiological concepts of selection bias, information
bias, intervention bias, and confounding and discusses ways in which these sources of bias can be
minimized.
Key words Epidemiology, Selection bias, Information bias, Intervention bias, Confounding, Validity
1 Introduction
The scope of clinical epidemiology is broad, ranging from the study

of the patterns and predictors of health outcomes in defined popu-
lations to the assessment of diagnostic and management options in
the care of individual patients. Moreover, the discipline encom-
passes such diverse topics as the evaluation of treatment effective-
ness, causality, assessment of screening and diagnostic tests, and
clinical decision analysis [1]. No matter what topic you are addres-
sing, there are two basic components to any epidemiological study:
exposure and outcome. The exposure can be a risk factor, a prog-
nostic factor, a diagnostic test, or a treatment, and the outcome is
usually death or disease [2]. Clinical epidemiology methods are
used to describe associations between exposures and outcomes.
The best research design for the investigation of causal relation-
ships is the randomized clinical trial. However, it is not always
feasible or ethical to perform such a study and under these circum-
stances, observational studies may be the best alternatives.
Patrick S. Parfrey and Brendan J. Barrett (eds.), Clinical Epidemiology: Practice and Methods, Methods in Molecular Biology,
vol. 2249, https://doi.org/10.1007/978-1-0716-1138-8_2, © Springer Science+Business Media, LLC, part of Springer Nature 2021
17
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Upon reaching home he went directly to his chamber, and was glad
to enter it without meeting his daughter. His reflection in the mirror
surprised him, as he expected to find a face thirty years older than
when it started for the village. But there were no outward traces of
the recent struggle. It was the same face, calm, firm, and as self-
reliant as ever. This was reassuring and did much toward a return of
confidence. He threw himself upon the bed, and as he lay there he
heard through the open window the voices of Molly and Amos in the
old-fashioned garden. They seemed very jolly and happy, and
Molly’s laughter came like music to his ears; but her companion,
although amusing and full of fun, seemed to do none of the laughing;
and then it came upon him that in all his intercourse with Amos he
had never heard him laugh. Ever ready to smile, and often irresistible
in his high spirits, yet he never laughed aloud. And the deep
melancholy of his face when in repose—was that a result of fulfilling
prophecies? Were there solemn secrets behind that boyish face?
The perfume of the flowers stole in through the closed blinds, and he
could hear the buzzing of a bee outside the window, mingling with
the voices in the garden. These voices became lower, the subject of
conversation having changed—perhaps to something more serious
—and Mr. Cabot took a nap.
VII
“DID you go to Silas Farnum’s?” was Molly’s first question, and her
father confessed having done precisely as Amos had predicted; but
while giving a truthful account of his experience, he told the story in a
half-jesting manner, attributing his compulsory visit to some hypnotic
influence, and to a temporary irresponsibility of his own. His
daughter, however, was not deceived. Her belief in a supernatural
agency renewed its strength.
As for her father, he had never been more at sea in the solution of a
problem. In his own mind the only explanation was by the dominance
of another mind over his own, by a force presumably mesmeric. The
fact that Amos himself was also a victim rendered that theory difficult
to accept, unless both were dupes of some third person. If at the
time of his visit to Silas Farnum he had been ill, or weak, or in a
nervous condition, or had it occurred at night when the imagination
might get the better of one’s judgment, there would have been the
possibility of an explanation on physical grounds. But that he, James
Cabot, of good health and strength, should, in the sunlight of a
summer noon, be the powerless victim of such an influence, was a
theory so mortifying and preposterous as to upset his usual
processes of reason.
It was not until the next afternoon that an opportunity was given for a
word with Amos. Out on the grass, beneath a huge elm at the
easterly corner of the house, Mr. Cabot, in a bamboo chair, was
reclining with his paper, when he noticed his young friend cantering
briskly along the road on a chestnut horse. Amos saw him, turned his
animal toward the low stone wall that separated the Cabots’ field
from the highway, cleared it with an easy jump and came cantering
over the grass.
“Is that old Betty? I didn’t know she was a jumper.”
“Oh, yes. She has a record.” Dismounting, he faced her about and,
with a tap on the flank, told her to go home. She returned, however,
and showed a desire to rub noses with him. “Well, have your way,
old lady,” and leaving her to a feast of clover he threw himself on the
ground at Mr. Cabot’s feet.
“You are a kind man to your animals, Amos, although you may be
somewhat offensive as a prophet.”
“So you went, after all?”
“Went where?”
“To see Silas Farnum.”
“Did I say that?”
Amos looked up with a smile that could have a dozen meanings. His
wily companion, from a sense of professional caution, wished to feel
his way before committing himself.
“You think I went, after all?”
“Yes, sir, I know you did, from my own experience.”
“Which is that the events inevitably occur as foreseen?”
“Always.”
“Well, I will make a clean breast of it and tell you just what
happened.”
“I know it already, Mr. Cabot, as well as if you had told me.”
“Do you know of my resolve not to do it? Of my ineffectual resistance
and the sensations I experienced?”
“I think so. I have been through it all myself.”
For a minute or two neither spoke. Amos, resting upon an elbow, his
cheek against the palm of one hand, was, with the other, deceiving a
very small caterpillar into useless marches from one end of a blade
of grass to the other. Mr. Cabot, in a more serious tone, continued:
“Can you tell me, Amos, on your honor, that as far as you know there
was no attempt on your part, or on the part of any other person, to
influence me upon that occasion?”
Amos tossed aside the blade of grass and sat up. “I give you my
word, sir, that so far as I know there is nothing in it of that nature. I
am just as helpless as you when it comes to any attempt at
resistance.”
“Then how do you account for it?”
Amos had plucked a longer blade of grass, and was winding it about
his fingers. “My explanation may seem childish to you, but I have no
better one to offer. It is simply that certain events are destined to
occur at appointed times, and that my knowing it in advance is not
allowed to interfere with the natural order of things.”
“The evidence may seem to point that way, judging from my own
experience, but can you believe that the whole human race are
carrying out such a cut-and-dried scheme? According to that theory
we are merely mechanical dummies, irresponsible and helpless, like
cogs in a wheel.”
“No, sir, we are at liberty to do just as we please. It was your own
idea going to Silas Farnum’s. That you happened to be told of it in
advance created an artificial condition, otherwise you would have
gone there in peace and happiness. In other words, it was ordained
that you should desire to do that thing, and you were to do as you
desired.”
The lawyer remained silent a moment, his face giving no indication
either of belief or denial.
“Have you never been able to prevent or even modify the fulfilment
of an act after having seen it in advance?”
“No, sir; never.”
“Then these scenes as presented to you are invariably correct,
without the slightest change?”
“Yes.”
Mr. Cabot looked down at his friend with a feeling that was not
without a touch of awe. Of the young man’s honesty he had not the
slightest doubt, and his own recent experience seemed but one
more proof of the correctness of his facts. He looked with a curious
interest upon this mysterious yet simple Oriental squatting idly on the
grass, his straw hat tilted back on his head, the dark face bent
forward, as with careful fingers he gathered a bunch of clover.
“If this faculty never fails you your knowledge of future events is
simply without limit. You can tell about the weather, the crops, the
stock market, the result of wars, marriages, births, and deaths, and
who the next president is to be.”
“Yes, sir,” he answered quietly, without looking up.
Mr. Cabot straightened up in his chair and rubbed his chin. His
credulity had reached its limit, yet, if he could judge by the evidence
already presented, the young man was adhering strictly to the truth.
There followed a silence during which Betty, who in nibbling about
had approached within a few feet of them, held out her head, and
took the clover from Amos. Mr. Cabot brought a pencil and piece of
paper from his pockets. “I would like to try one more experiment, with
your permission. Will you write on that paper what I am to do at—
well, say ten o’clock to-night?”
Amos took the paper and closed his eyes, but in a moment looked
up and said, “You are in the dark and I can see nothing.”
“Then you have no knowledge of what goes on in the dark?”
“No, sir; only of things that I can see. If there is any light at all I can
see as if I were there in person, but no better. To-night at ten o’clock
you are in your own chamber, and it is absolutely black.”
“Then change the hour to six o’clock.”
As Mr. Cabot, a moment later, turned a sidelong glance toward his
friend, sitting with closed eyes before him, he thought the little mark
upon his forehead had never been so distinct. He regarded it with a
mild surprise as it seemed almost aglow; but the sky was becoming
rosy in the west, and there might be a reflection from the setting sun.
Amos wrote something on a slip of paper, folded it up and returned it
to Mr. Cabot, who carefully tucked it away in a pocket saying, “I shall
not read it until six-thirty. I will tell you to-morrow if you are correct.”
“Oh, that is correct, sir! You need have no anxiety on that point.”
As he spoke there passed slowly along the road a cart containing
two men, and behind the cart, securely fastened, walked a heavy,
vicious-looking bull.
“That is an ugly brute,” he said.
“So I was just thinking. Does he belong in the town?”
“Yes; it is Barnard’s bull. Yesterday he got loose and so mutilated a
horse that it had to be shot; and within an hour he tried his best to kill
old Barnard himself, which was a good undertaking and showed
public spirit. He is sure to have a victim sooner or later, and it
certainly ought to be old Barnard if anybody.”
“Who is Barnard?”
“He is the oyster-eyed, malignant old liar and skinflint who lives in
that red house about a mile below here.”
“You seem to like him.”
“I hate him.”
“What has he done to you?”
“Nothing; but he bullies his wife, starves his cattle, and cheats his
neighbors. Even as a small boy I knew enough to dislike him, and
whenever he went by the house I used to stone him.”
“What a pleasant little neighbor you must have been!”
Amos tried to smile, but his anger was evidently too serious a matter
to be treated with disrespect. Mr. Cabot, after regarding for a
moment the wrathful eyes that still followed the bull, continued:
“You are more than half barbarian, my war-like farmer. Must you do
physical damage to everyone you dislike?”
“No, sir; but as a rule I should like to. As for loving your enemies—
count me out. I love my friends. The man who pretends to love his
enemies is either a hypocrite or a poor hater.”
The older man smiled at the earnestness with which this sentence
was uttered. “I am afraid, Mr. Amos Judd, you are not a Christian.
Take my advice and join a bible-class before the devil gets his other
hand upon you.”
After a few words on other matters, Amos called his mare, and
departed.
As the hour of six drew near, Mr. Cabot made a point of realizing that
he was a free agent and could do whatever he wished, and he
resolved that no guess, based on a probability, should prove correct.
To assure himself that there was no compulsion or outside influence
of any nature, he started first for the barn to execute a fantastic
resolve, then as an additional proof that he was absolutely his own
master, suddenly changed his mind, turned about, and went upstairs.
Going along a back passage with no definite intention, he paused at
a half-open door, looked in, and entered. The blinds were closed, but
between the slats came bars of light from the western sun, illumining
the little room, an unused chamber, now serving as a storehouse for
such trunks and sundry relics as had failed to reach the attic. Mr.
Cabot noticed a rocking-horse in one corner and his eyes sparkled
with a new idea. After closing the door he dragged the steed from its
resting-place, planted it in the middle of the floor, and looked at his
watch. It lacked four minutes of six. As he prepared to mount he saw
the legs of a rag-baby projecting over a shelf, and pulling her down,
could not restrain a smile as he held her in his arms. A large, round,
flat, and very pale but dirty face was emphasized by fiery cheeks,
whose color, from a want of harmony with the coarse material of her
visage, had only lingered in erratic blotches. With this lady in his
arms he mounted the horse, and, while gently rocking with both feet
on the ground, he again took out his watch and found he was just on
the minute of six o’clock. But he kept his seat for a moment longer,
judging the situation too good to be trifled with, and too unusual for
any ordinary guess. Carelessly he rocked a little faster, when a front
foot of his overladen steed slipped from its rocker and Mr. Cabot
nearly lost his balance. The damage, however, he easily repaired;
the rag-baby was replaced upon her shelf, and when he left the little
room and returned to his own chamber there was an expression
upon his face that seemed indicative of an amiable triumph. Some
minutes later, with a similar expression, he took from his pocket the
slip of paper on which Amos had written, read it once with some
haste, then a second time and more carefully.
The Hon. James Cabot, one of the most respected
residents of Daleford, attempted at six o’clock to elope
with an obscure maiden of the village. But his horse, an
animal with one glass eye and no tail, broke down before
they had fairly started and went lame in his off front foot.
Gently rocking with both feet on the ground
For several minutes he stood looking down at the paper between his
fingers, occasionally drawing a hand across his forehead. Then he
refolded the paper and placing it in his pocket, took his hat and went
out into the orchard, to think, and to be alone.
On questioning Amos he found no more light was to be expected
from that quarter, as the young man had already expounded his only
theory, which was that these visions were but optional warnings of
the inevitable: that all was fore-ordained: that there could be no
variations in the course of Fate. His mind was not philosophical; his
processes of reason were simple and direct, and he listened with
profound interest to Mr. Cabot’s deeper and more scientific attempts
at reaching a consistent explanation. Little progress, however, was
made in this direction, and the lawyer admitted that the evidence, so
far, contradicted in no detail his friend’s belief. He also found that
Amos, although deeply concerned in the subject when once opened,
rarely introduced it himself or referred to it in any way; and that he
never employed his power except in the rarest emergencies.
Moreover, the lawyer understood how such a faculty, although of
value in certain cases, would, in the great majority, be worse than
useless, while it could not fail of an overpowering influence on the
being who employed it. He respected the strength of purpose that
enabled the young man to keep it in the background, and he felt that
he had discovered at least one reason for the restless pleasures of
his youth. Now, happily, he was securing a calmer and a healthier
diversion from a life in the open air. As his neighbor became the
object of a deeper study it was evident the conflicting qualities that
seemed to give such varying colors to his character were the result
of these extraordinary conditions. His occasional recklessness and
indifference were now easily explained. His disregard for religious
observances was in perfect harmony with an insight into the
workings of a stupendous fate, immeasurably above the burning of
candles and the laws of ecclesiastical etiquette. His love of exercise,
of sunshine, of every form of pleasure and excitement, were but the
means of escape from the pursuing dread of an awful knowledge.
And the lavish generosity that often startled his friends and
bewildered Daleford was a trivial matter to one who, if he cared to
peruse in advance the bulletins of the stock exchange, could double
his fortune in a day.
Off and on through July and a part of August an unwonted animation
prevailed at the Cabots’, extending at times along the maples to the
other house. Certain visitors of Molly’s were the cause of this gayety,
and in their entertainment she found Amos a helpful friend. His
horses, his fields, his groves, his fruits, his flowers, and himself, were
all at her disposal, absolutely and at any time. A few friends of his
own coming at the same period proved a welcome reinforcement,
and the leaves of the old maples rustled with a new surprise at the
life and laughter, the movement, the color, and the music that
enlivened their restful shades. And also at night, during the warm
evenings when farmers were abed, the air was awake with melodies
which floated off in the summer air, dying away among the voices of
the frogs and turtles along the borders of the meadow.
One warm afternoon in August, when there were visitors at neither
house, Amos and Molly climbed over a wall into a pasture, for a
shorter cut toward home. The pasture was extensive, and their
course lay diagonally across a long hill, beyond whose brow they
could see nothing. A crimson sunshade and white dress were in
dazzling contrast to the dull greens of the pasture, whose prevailing
colors were from rocks and withered grass. Patches of wild bushes
where the huckleberries were in overwhelming majority necessitated
either wide detours or careful navigating among thorns and briars.
Her companion seemed indifferent to the painful fact that
knickerbockers are no protection against these enemies. But pricks
in the leg at the present moment were too trivial for notice. He was
speaking with unusual earnestness, keeping close at her side, and
now and then looking anxiously into her face. It may have been the
heat and the exercise that drove the color to her cheeks, and there
were also signs of annoyance as if she desired to escape him; but
the ground was uneven, and the stones and bushes rendered haste
impossible. She also appeared tired, and when they stopped at
intervals always turned away her face, until finally, when half across
the field, she sank upon a rock. “I really must rest. I am dreadfully
warm.”
He stood beside her, facing in the same direction, both looking over
the peaceful valley from which an occasional cow-bell was the only
sound.
“It is really a little unfair that my old record should come between us.
I was only twenty then, with no end of money and no parents or
guardian to look after me. Mr. Judd would let me do whatever I
wished, and of course I sailed ahead and did everything. Instead of
having an allowance like other fellows I just asked for what I wanted,
and always got it. And that is death to a boy.”
He pulled a twig from a bush and began to bite the end of it. If at that
instant he had glanced down at the face beside him, he might have
detected an expression that was not unjustly severe. There was a
distinct ray of sympathy in the eyes that were fixed thoughtfully upon
the valley.
“And then all the girls met me more than half-way, as if they, too, had
conspired against me.”
This was said in a half-resentful, half-plaintive tone, and so
delightfully free from any boastfulness that Molly, to conceal
something very near a smile, bent her head and picked nettles from
her skirt.
“Of course I liked a good time, there is no denying that, and I struck
the wrong gang at college. I suppose I was weak—everlastingly and
disgustingly weak; but really you might make allowances, and
anyway—”
He stopped abruptly and turned about. Looking up she saw an
expression in his eyes, as they gazed at something behind her, that
caused her to spring to her feet and also turn about. As she did so
the color left her face and her knees gave way beneath her.
Instinctively she clutched his arm. Within twenty yards of them stood
Barnard’s bull, and in his broad black head and cruel horns, in the
distended nostrils and bloodshot eye, she read the fury of an
unreasoning brute; and with it her own death and mutilation.
Helpless they stood in the open pasture with no tree or refuge near.
Amos cast a swift glance to the right, to the left, and behind them.
The bull lowered his head just a very little, and as he stepped slowly
forward she could hear his breath in impatient puffs. Her brain began
to swim and she closed her eyes, but a sharp word and a rough
shake brought her back with a start.
“Do just as I tell you. Turn and walk slowly off to the wall at the right.
Then climb over. Don’t run till I say so. Give me your parasol.”
He twisted her about and gave her a push.
“Don’t look around.”
Gasping, faint, and so weak from terror that she could hardly direct
her steps, she did as she was told. In her dazed mind there was no
conception of time or distance, but, a moment after, hearing a snort
from the bull and the quick pounding of his feet, she stopped and
turned. She expected to see Amos on the creature’s horns, but
Amos was running in the other direction, so far safe, although
scarcely his own length ahead. In an instant she saw to her horror
that, although a nimble runner, he was losing distance with every
spring of the bull. But with a presence of mind that did much toward
renewing her own courage, he kept looking over his shoulder, and
when further running was hopeless, he jumped swiftly to one side,
the side up the hill, and the ponderous brute plunged on for several
feet before he could come to a stop. Amos looked at once in her
direction, and when he saw her he shook his hand and cried, in an
angry voice:
“Run! Run! Your life depends on it!”
There was no time to say more, for the bull had wheeled and was
again coming toward him. Molly turned and ran as she never ran
before, and never before did so many thoughts flash through her
mind. Above all came the torturing regret that she could be of no
possible service to the man who, at that moment perhaps, was
giving up his life for hers. Leaping rocks, stumbling over hillocks,
tearing through bushes, she finally reached the wall, scrambled up
and over as best she could, then, with a throbbing heart and pallid
face, looked back into the field.
They were farther up the hill, and Amos had evidently just jumped
aside, for again the bull and he were facing each other. The animal
was advancing slowly toward him, head down, with an angry lashing
of the tail and occasional snorts that drove the blood from the
spectator’s heart. As Amos retreated slowly, his face to the animal,
she saw him look swiftly in her direction, then back at the bull. Faster
and faster the animal came toward him, and when finally he bounded
forward on a run Amos turned and ran for his life. He was now
making for this side of the pasture, but she saw with the keenest
anguish that all his elasticity had departed, that he was losing ground
much faster than at first. That he should show signs of exhaustion
caused her no surprise, for the ground was rough, low briars and
bushes concealing rocks of treacherous shapes and varying sizes,
and the race was harder for the man than for the bull. The distance
between them was being lessened with a rapidity that might end the
struggle without a second’s warning, and the horns were now within
a yard of his heels. Again he jumped to one side, but this time it
brought a cry of agony from beyond the wall. His foot slipped, and
instead of landing a yard or more from the creature’s path, he
measured his length upon the ground. The bull lowered his head and
plunged savagely upon him. The horns grazed the prostrate body,
and the heavy brute, by his own impetus, dashed a dozen yards
beyond. Amos raised first his head and shoulders, then climbed to
his feet, slowly, like one bewildered or in pain. He stood cautiously
upon his legs as if uncertain of their allegiance, but he still clutched
the crimson sunshade. The bull, with fiery nostrils and bloodshot
eyes, once more came on, and Amos started for the wall. It was
evident to the one spectator that his strength was gone. With every
jump of the thing behind him he was losing ground, and the awful
end was near, and coming swiftly. She sank against the wall and
clutched it, for the sky and pasture were beginning to revolve before
her straining eyes. But Amos, instead of coming straight for the wall,
bore down the hill. With the hot breath close upon his heels, he
opened the crimson sunshade, jumped aside, and thrust it upon the
pursuing horns: then without looking back he made a bee-line for the
wall. It was skilfully done, and for one precious moment the seeming
victor was delayed by goring the infuriating color; but only for a
moment. He saw his enemy escaping and bounded in pursuit. This
time, however, he missed him by a dozen feet and saw him vault the
barrier into safety. The wall he accepted as a conclusion, but he
stood close against it, looking over in sullen anger, frothing, hot-
eyed, and out of breath.
Then he witnessed a scene, to him of little interest, but which
signified much to another person. He saw the girl, anxious, pale, with
disordered hair, eagerly approach the exhausted runner; then,
nervously pressing a hand to her cheek, she bent forward and asked
a question. The young man, who was leaning against a tree and
seemed to have trouble with his breathing, suddenly, with a joyful
face, stretched forth his hands, and with even more eagerness than
her own, asked in his turn a question, whereupon the color rushed to
her face. Looking down, then up at him, then down again, she smiled
and muttered something, and he, without waiting for further words,
seized her in his arms, and with one hand holding her chin, kissed
her mouth and cheeks, not once but many times. But she pushed
away from him, flushed and possibly angry. However, it could not
have been a deep-seated or lasting anger, for she created no
disturbance when he took one of her hands in both of his and made
a little speech. It appeared an interesting discourse, although she
looked down and off, and all about, at everything except at him,
smiling and changing color all the while. He seemed foolishly happy,
and when a moment later he wished to assist in rearranging her hair,
he was not depressed because the offer was declined with
contempt.
Then the young man took a few steps toward the wall, and stood
facing the huge head whose bloodshot eyes were still upon him. As
he lifted his hand there was a hitch in the motion, and a spasm of
pain drew down a corner of his mouth, but the girl behind him could
not see this. He raised his cap and saluted his adversary.
“I thank you, Bull, for chasing me into Molly Cabot’s heart”
“I thank you, Bull, for chasing me into Molly Cabot’s heart.”
Then he turned, and hand in hand, the two people disappeared
among the pines.
VIII
ACCORDING to habit, Mr. Cabot composed himself by the library
table that evening for an hour’s reading before going to bed, but the
book was soon lifted from his grasp and Molly seated herself in his
lap. Although fingers were inserted between his collar and neck as a
warning that the closest attention was expected, there followed a
short silence before any words were uttered. Then she told him all:
of being face to face with Barnard’s bull; of the narrow escape; of
how Amos remained alone in the open field, and lastly, she gave the
substance of what the rescuer had said to her, and that she had
promised to be his wife. But on condition that her father should
consent.
He received the news gravely; confessed he was not so very much
surprised, although he had hoped it would come a little later. And
she was very happy to find he made no objection to Amos as a son-
in-law, and to hear him praise his character and pronounce him an
honest, manly fellow. His behavior with the bull was heroic, but did
not she think the reward he demanded was exorbitant? Was it not a
little greedy to ask as a price for his services the entire value of the
rescued property? It certainly was not customary to snatch away the
object before placing it in the owner’s hands. “But he risked his life to
save yours, and for that he shall have anything I own.”
The following morning, as she stepped upon the piazza, the doctor’s
buggy came down the opposite avenue and turned toward the
village. Could old Mrs. Judd be ill? or was it one of the servants?
An hour later, as there were still no signs of her bull-fighter she
began to feel a slight annoyance. Perhaps after sleeping upon the
events of yesterday his enthusiasm had cooled. Perhaps his
exceptionally wide experience in this field had taught him that the
most delicate way out of such dilemmas was to give the girl the
initiative, and perhaps, now that he was sure she loved him, all the
fun had departed. Perhaps, in short, he was now realizing that he
had committed himself. Although none of these suspicions took a
serious hold there was a biting of the nether lip and a slight flush
upon the cheeks as she re-entered the house: and in order that he
might not suspect, when he did come, that his delay had caused the
slightest feeling, or that anyone had watched for him, she returned to
her room. A few moments later a note was brought in which was
received with indifference, but which, after Maggie’s departure she
opened with nervous fingers.
MY Girl: That bull, God bless him! smashed two of my
ribs, the doctor says, but I know better. They were broken
by an outward force, a sudden expansion of the heart, and
I felt them going when you came into a pair of arms.
Please come over, or I shall fly away, as I feel the
sprouting of wings, and there is a cracking among the
other ribs.
Amos.
She went, and although their conversation that morning touched
upon ribs and anatomy, it would, if taken as a whole, have been of
little value to a scientist. It was distinctly personal. The one sentiment
which appeared to have an irresistible fascination for the bull-fighter
and his fiancée colored all remarks, and the fact that the dialogue
would have caused them the most intense mortification if made
public, tended in no degree to lessen their enjoyment. To a middle-
aged person who had never been in love it would have been
unendurable.
Later in the day she intercepted the doctor and learned as much as
possible of the patient’s condition. Two ribs were badly broken, he
said; had been pressed inward to a serious extent, but so far there
were no indications of internal injuries. Of this, however, he could not
at present be absolutely sure, but he thought there was no great
cause for alarm. The patient, of course, must keep quiet for a week
or two.
Fortunately for Amos there proved to be no injury save the damaged
ribs, but three long weeks elapsed before he was allowed to go up
and down stairs and move about the house.
The last day of August proved a day of discoveries.
It was bright and warm, yet invigorating, the perfection of terrestrial
weather, and Mr. Cabot and Molly, early in the afternoon, were sitting
upon the piazza discussing the date of their departure, Amos
occupying his favorite place upon the floor in front of them, his back
against a column. When she informed her father that additional
trunks or boxes of some kind would be needed, Amos said that such
articles were going to waste in the Judd residence, and if she would
but step across the way and select a few, it would be a lasting
benefit to an overcrowded attic. This offer was accepted and they
started off. After climbing the final stairs, which were steep and
narrow, Molly seated herself upon an old-fashioned settle, the back
of which could be lowered and used as an ironing table. “How I do
love this smell of an attic! Is it the sap from the hot pine? And isn’t
there sage in the air, or summer savory?”
“Both. With a few old love-letters and a touch of dried apples.”
“Whatever it is, I love it. The days of my childhood come galloping
back,” and with upturned face she closed her eyes and drew a
longer breath. He bent silently over and touched her lips.
“What a breach of hospitality!”
“When a visitor insults a host by sleeping in his presence, it is
etiquette to awaken her. And when lips with those particular
undulations look one pleasantly in the eye and say ‘Amos, kiss us,’
what do you expect to happen?”
“From you I expect the worst, the most improper thing.”
“And you will always get it, O spirit of old-fashioned Roses!”
In opening a window he disturbed an enormous fly, whose buzzing
filled every corner of the roof. “To me,” he said, “this atmosphere
recalls long marches and battles, with splendid victories and awful
defeats.”

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Clinical Epidemiology Practice and

Methods 3rd Edition Patrick S Parfrey

Concepts of epidemiology : integrating the ideas,

Linux Pocket Guide Essential Commands 3rd Edition

Complications of Regional Anesthesia Principles of Safe

Clinical assessment and diagnosis in social work

Teaching Epidemiology A guide for teachers in

Cancer Epidemiology and Prevention 4th Edition Michael

Sample Sizes for Clinical, Laboratory and Epidemiology

Epidemiology and Biostatistics An Introduction to

For further volumes:

Practice and Methods

Patrick S. Parfrey and Brendan J. Barrett

ISSN 1064-3745 ISSN 1940-6029 (electronic)

© Springer Science+Business Media, LLC, part of Springer Nature 2021

St. John’s, NL, Canada Patrick S. Parfrey

1 On Framing the Research Question and Choosing the Appropriate

15 Randomized Controlled Trials 5: Biomarkers and Surrogates/Outcomes . . . . . . 261

30 Changing Health-Related Behaviors 2: On Improving the Value

and Biostatistics, Faculty of Health Sciences, McMaster University, Hamilton, ON,

PIETRO RAVANI • Division of Nephrology, Department of Medicine, University of Calgary,

On Framing the Research Question and Choosing

Clinical epidemiology is the science of human disease investigation,

2 Framing the Clinical Research Question

The research process usually starts with a general idea or initial

reading the literature and thinking of ways to extend or refine

studies (Does it work in the real world?), and trade-offs between

The goal of clinical research is to estimate population characteristics

There are two main types of error: random or accidental error,

random sampling, possibly over-sampling some subgroup of par-

5 Sample Size Estimation

When planning a comparative study, two possible random errors

P value of 0.05). A Type II error is made if the results of a study are

Surrogate marker Hard end point

Fig. 3 Validity issues for a surrogate end point to be tested in a RCT

definition of the primary and secondary outcome measures; how

7 External and Internal Validity

The operational criteria applied in the design influence the external

minimized. Selection, measurement, and confounding biases can

8 Clinical Relevance vs. Statistical Significance

The concepts of clinical relevance and statistical significance are

Fundamental to evidence-based healthcare is the concept of “hier-

control studies where the direction of the study is reversed. Partici-

10 Experimental Designs for Intervention Questions

The RCT design is appropriate for assessment of the clinical effects

ACE inhibitor) or when a new therapy is already known to be

11 Designs for Diagnostic Questions

When assessing a diagnostic test, the reference or “gold standard”

Diagnostic question Direction Design Problems Example Reference

12 Maximizing the Validity of Nonexperimental Studies

When randomization is not feasible, the knowledge of the most

Adequate reporting is critical to the proper interpretation and

Bias in Clinical Research

The scope of clinical epidemiology is broad, ranging from the study

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