Guide to

Evaluating the Effectiveness of Strategies for

Preventing Work Injuries:

How to Show Whether a Safety Intervention Really Works

Lynda S. Robson, Harry S. Shannon, Linda M. Goldenhar, Andrew R. Hale

DEPARTMENT OF HEALTH AND HUMAN SERVICES

Public Health Service

Centers for Disease Control and Prevention

National Institute for Occupational Safety and Health

April 2001
ii

DISCLAIMER

Mention of any company name or product does not constitute endorsement by the

National Institute for Occupational Safety and Health.

This document is in the public domain and may be freely copied or reprinted.

Copies of this and other NIOSH documents are available from NIOSH.

For information about occupational safety and health topics contact NIOSH at:

1-800-35-NIOSH (1-800-356-4674)

Fax: 513-533-8573

E-mail: pubstaft@cdc.gov

www.cdc.gov/niosh

National Institute for Occupational Safety and Health

Publications Dissemination

4676 Columbia Parkway

Cincinnati, OH 45226-1998

For information about the Institute For Work & Health and its research:

416-927-2027

Fax: 416-927-2167

E-mail: info@iwh.on.ca

www.iwh.on.ca

DHHS (NIOSH) Publication No. 2001-119
Table of Contents

Acknowledgements ................................................................................................................................. ix

Preface ........................................................................................................................................................ xi

Information About Authors....................................................................................................................... xiii

Chapter 1 Introduction: Safety Intervention Effectiveness Evaluation ................................... 1

1.1 What is a safety intervention? ........................................................................................ 1

1.2 Effectiveness evaluation .................................................................................................. 2

1.3 Overview of the evaluation process and the guide .................................................... 2

1.4 Other types of evaluations .............................................................................................. 3

Chapter 2 Planning Right from the Start ....................................................................................... 5

2.1 Introduction ...................................................................................................................... 6

2.2 Defining the scope of the evaluation ............................................................................. 6

2.3 Who should be involved with the evaluation? ............................................................ 6

2.3.1 Evaluation committee ......................................................................................................... 6

2.3.2 Internal vs. external evaluators .......................................................................................... 7

2.3.3 Technical or methodological expertise ................................................................................. 7

2.4 Models to assist planning ...................................................................................................... 8

2.4.1 Conceptual models .............................................................................................................. 8

2.4.2 Program logic models .......................................................................................................... 10

2.5 Quantitative vs. qualitative methods for collecting evaluation data ........................ 11

2.6 Choosing the evaluation design ........................................................................................... 12

2.6.1 Strength of evidence provided by different evaluation designs ........................................... 13

2.6.2 Ethical considerations ......................................................................................................... 14

2.7 Practical tips ...................................................................................................................... 14

2.7.1 Time management ............................................................................................................... 14

2.7.2 Dealing with reaction to interim results ............................................................................. 14

2.7.3 Intervention diary ............................................................................................................... 14

2.7.4 Getting cooperation of workplace parties ............................................................................ 15

2.8 Summary ........................................................................................................................... 15

Chapter 3 Before-and-after design: A simple evaluation design ............................................. 17

3.1 Introduction ...................................................................................................................... 18

3.2 Design terminology ......................................................................................................... 18

3.3 Non-experimental designs .............................................................................................. 18

3.4 Before-and-after design ................................................................................................... 19

iii
3.5 Threats to internal validity of before-and-after designs ......................................... 19

3.5.1 History threat ...................................................................................................................... 20

3.5.2 Instrumentation/reporting threat ....................................................................................... 22

3.5.3 Regression-to-the-mean threat ............................................................................................ 23

3.5.4 Testing threat ...................................................................................................................... 24

3.5.5 Placebo and Hawthorne threats .......................................................................................... 25

3.5.6 Maturation threat ............................................................................................................... 26

3.5.7 Dropout threat ..................................................................................................................... 26

3.6 Summary 27

Chapter 4 Quasi-experimental and experimental designs: more powerful 

evaluation designs ........................................................................................................... 29

4.1 Introduction ...................................................................................................................... 30

4.2 Quasi-experimental designs ........................................................................................... 30

4.2.1 Strategy #1: Add a control group (e.g., pre-post with non-randomized control) ............... 30

4.2.2 Strategy #2: take more measurements (time series designs) ............................................... 32

4.2.3 Strategy #3: Stagger the introduction of the intervention (e.g., multiple baseline ...........

design across groups) .................................................................................................... 33

4.2.4 Strategy #4: Reverse the intervention ............................................................................... 35

4.2.5 Strategy #5: Measure multiple outcomes .......................................................................... 35

4.3 Experimental designs ...................................................................................................... 37

4.3.1 Experimental designs with “before” and “after” measurements ....................................... 37

4.3.2 Experimental designs with “after”-only measurements .................................................... 39

4.4 Threats to internal validity in designs with control groups ....................................... 40

4.4.1 Selection threats .................................................................................................................. 40

4.4.2 Selection interaction threats ................................................................................................ 40

4.4.3 Diffusion or contamination threat .................................................................................... 41

4.4.4 Rivalry or resentment threat ............................................................................................... 41

4.5 Summary ........................................................................................................................... 42

Chapter 5 Study sample: Who should be in your intervention and evaluation? ................... 43

5.1 Introduction ...................................................................................................................... 44

5.2 Some definitions ............................................................................................................... 44

5.3 Choosing people, groups or workplaces for the study sample ................................ 44

5.3.1 How to choose a (simple) random sample ........................................................................... 45

5.3.2 How to choose a stratified random sample .......................................................................... 47

5.4 Randomization - forming groups in experimental designs ....................................... 48

5.4.1 Why randomize? ................................................................................................................. 48

5.4.2 Randomized block design and matching ............................................................................. 49

5.5 Forming groups in quasi-experimental designs .......................................................... 49

5.6 Summary ........................................................................................................................... 50

Table of Contents

iv
Chapter 6 Measuring outcomes ....................................................................................................... 51

6.1 Introduction ...................................................................................................................... 52

6.2 Reliability and validity of measurements ..................................................................... 52

6.3 Different types of safety outcome measures ................................................................ 54

6.3.1 Administrative data collection - injury statistics ............................................................... 54

6.3.2 Administrative data collection - other statistics ................................................................. 58

6.3.3 Behavioral and work-site observations ................................................................................ 59

6.3.4 Employee surveys ................................................................................................................ 60

6.3.5 Analytical equipment measures .......................................................................................... 62

6.3.6 Workplace audits ..................................................................................................................... 62

6.4 Choosing how to measure the outcomes ...................................................................... 62

6.4.1 Evaluation design and outcome measures .......................................................................... 62

6.4.2 Measuring unintended outcomes ........................................................................................ 64

6.4.3 Characteristics of measurement method ............................................................................. 64

6.4.4 Statistical power and measurement method ....................................................................... 65

6.4.5 Practical considerati............................................................................................................. 65

6.4.6 Ethical aspects ..................................................................................................................... 65

6.5 Summary ........................................................................................................................... 65

Chapter 7 Qualitative methods for effectiveness evaluation: 

When numbers are not enough ..................................................................................... 67

7.1 Introduction ...................................................................................................................... 68

7.2 Methods of collecting qualitative data .......................................................................... 68

7.2.1 Interviews and focus groups ............................................................................................... 68

7.2.2 Questionnaires with open-ended questions ........................................................................ 70

7.2.3 Observations ....................................................................................................................... 70

7.2.4 Document analysis .............................................................................................................. 70

7.3 Ways to use qualitative methods in effectiveness evaluation .................................... 71

7.3.1 Identifying implementation and intermediate outcomes .................................................... 71

7.3.2 Verifying and complementing quantitative outcome measures .......................................... 71

7.3.3 Eliminating threats to internal validity .............................................................................. 72

7.3.4 Identifying unintended outcomes ....................................................................................... 72

7.3.5 Developing quantitative measures ...................................................................................... 72

7.4 Selecting a sample for qualitative purpose .................................................................. 73

7.5 Qualitative data management and analysis ................................................................. 74

7.6 Ensuring good quality data ............................................................................................ 75

7.7 Summary ................................................................................................................................. 76

Table of Contents

v
Chapter 8 Statistical Issues: Are the results significant? ........................................................... 77

8.1 Introduction ...................................................................................................................... 78

8.2 Why statistical analysis is necessary ............................................................................. 78

8.3 P-values and statistical significance .............................................................................. 79

8.4 Statistical power and sample size ................................................................................. 80

8.5 Confidence intervals ........................................................................................................ 81

8.6 Choosing the type of statistical analysis ....................................................................... 82

8.6.1 Type of data ......................................................................................................................... 82

8.6.2 Evaluation design ............................................................................................................... 83

8.6.3 Unit of analysis ................................................................................................................... 84

8.7 Avoiding pitfalls in data analysis .................................................................................. 84

8.8 Summary ........................................................................................................................... 84

Chapter 9 Summary of recommended practices ........................................................................... 85

9.1 Introduction ....................................................................................................................... 85

9.2 Summary of recommended practices............................................................................. 86

Glossary ...................................................................................................................................................... 89

Appendix A Some models to assist in planning ............................................................................... 93

A.1 A model for interventions in the technical sub-system .............................................. 93

A.2 Models for interventions in the human sub-system ................................................... 95

A.3 Models for interventions in the safety management system ..................................... 97

Appendix B Examples of statistical analyses .................................................................................... 101

B.1 Analyses for before-and-after designs .......................................................................... 102

B.1.1 Before-and-after design with injury rate data...................................................................... 102

B.1.2 Before-and-after design with continuous data .................................................................... 104

B.2 Analyses with pre-post measures and a control group .............................................. 105

B.2.1 Pre-post with control group and rate data .......................................................................... 105

B.2.2 Pre-post with control group and continuous data .............................................................. 108

B.3 Analyses for designs with after-only measures and a control group ....................... 108

B.3.1 After-only measurements with two groups and rate data .................................................. 108

B.3.2 After-only measurements with several groups and rate data ............................................. 108

B.3.3 After-only measurements with two groups and continuous data ...................................... 109

B.3.4 After-only measurements with several groups and continuous data ................................. 109

B.4 Multiple measurements over time ................................................................................. 110

Table of Contents

vi
Table of Contents

vii

Appendix C Reporting your evaluation results ................................................................................ 113

C.1 Introduction ...................................................................................................................... 113

C.2 Evaluation report .............................................................................................................. 113

C.2.1 Structure of the report ......................................................................................................... 113

C.2.2 Audience specificity ............................................................................................................ 115

C.2.3 Clear language .................................................................................................................... 115

C.3 Communication beyond the report ............................................................................... 116

C.4 Summary ........................................................................................................................... 116

Bibliography .....................................................................................................................................................117

Acknowledgements

The idea for this guide arose in a meeting of the Scientific Committee on Accident Prevention (SCOAP)

at the International Commission on Occupational Health (ICOH) meeting in Tampere, Finland, July 1997. 

The co-authors thank the many individuals and organizations which gave valuable feedback to draft

versions of the Guide. These include: other members of the NORA Intervention Effectiveness Team (in

particular, Larry Chapman, Catherine Heaney, Ted Katz, Paul Landsbergis, Ted Scharf, Marjorie Wallace);

other SCOAP Committee members (Tore Larsson, Jorma Saari); additional academic colleagues (Donald

Cole, Xavier Cuny, Michel Guillemin, Richie Gun, Gudela Grote, Per Langaa Jensen, Urban Kjellén,

Richard Wells); individuals within Ministries or Departments of Labour (Brian Zaidman, Barry Warrack),

the Workplace Safety Insurance Board of Ontario (Richard Allingham, Marian Levitsky, Kathryn

Woodcock), Workers’ Compensation Board of BC (Jayne Player), and Workplace Health, Safety and

Compensation Commission of New Brunswick (Susan Linton); representatives of Ontario Safe Workplace

Associations (Dave Snaith (Construction), Linda Saak and R. Stahlbaum (Electrical & Utilities), James

Hansen (IAPA), Louisa Yue-Chan (Services), Mark Diacur (Transportation)); Irene Harris and members

of the Occupational Health and Safety Committee of the Ontario Federation of Labour; Mary Cook,

Occupational Health Clinics for Ontario Workers. Institute members who shared reference materials are

also thanked - John Lavis and Dorcas Beaton - as is Linda Harlowe (IWH), who constructed all of the

detailed graphical figures.

The final word of acknowledgement goes to the existing body of evaluation expertise that we drew upon

and adapted to a safety application. We are especially indebted to the classic works of Cook and Campbell

[1979] and Patton [1987, 1990].

ix

Preface

Our aim in this book is to provide students, researchers and practitioners with the tools and concepts

required to conduct systematic evaluations of injury prevention initiatives and safety programs. Successful

evaluations will advance the discipline of occupational safety by building a body of knowledge, based

on scientific evidence, that can be applied confidently in the workplace. This knowledge will provide a

solid foundation for good safety practice, as well as inform the development of standards and regulations.

Building such a knowledge base will help practitioners avoid the temptation of adopting safety procedures

simply because they appear “intuitively obvious” when no scientific evidence actually exists for those

practices. 

Users of the guide are encouraged to demonstrate the strongest level of evidence available for an

intervention by measuring the effect on safety outcomes in an experimental design. Even when this level

of evidence is not obtained, much useful information can still be gained by following the recommendations

in the book. In doing so, the safety field will become current with other disciplines, such as clinical

medicine, where evaluation information is increasingly available and allows for evidence-based decisionmaking. 

We hope that this guide will assist safety specialists to meet the challenge of effectiveness evaluations.

Please let us know if you found it useful by completing the evaluation form provided at the end to the

document.

xi

Information About Authors

Linda M. Goldenhar

Linda Goldenhar is a Research Psychologist at the National Institute for Occupational Safety and Heath.

She received her Ph.D. in Health Behavior at the University of Michigan. Her interests include intervention

research, quantitative and qualitative data collection methods, work-organization, job stress, and women’s

health. She is currently the team leader for the NIOSH NORA Intervention Effectiveness Research team.

The mission of the team is to educate occupational researchers about intervention research issues and to

encourage the development, implementation, and evaluation of occupational safety and health

interventions. Linda has published numerous peer-reviewed articles and delivered conference

presentations covering a wide array of occupational health-related and behavioral topic areas. She is on

the editorial board of Health Education and Behavior and Journal of Safety Research.

Andrew R. Hale

Andrew Hale is professor of Safety Science at the Delft University of Technology in the Netherlands and

editor of the journal Safety Science. His background is as an occupational psychologist. He worked for

18 years in the UK at the National Institute of Industrial Psychology and later at the University of Aston

in Birmingham. His experience in research in safety and health began with studies of accidents and

human error in industry and moved later into studies of risk perception, safety training and more recently

safety management and regulation. Since moving to Delft from Aston he has expanded his area of research

applications from industry to include transport (road, water and air), hospitals and public safety.

As editor of Safety Science and as a reviewer for both this journal and a number of others he is responsible

for assessing the articles presented for publication. In that capacity he has seen at close quarters the need

for improvement in the quality and application of the research and analysis methods used in safety

science.

Lynda S. Robson

Lynda Robson is a Research Associate at the Institute for Work & Health, Toronto, Canada. She obtained

her Ph.D. in Biochemistry from the University of Toronto, working afterwards in research labs. More recent

experience includes graduate-level training in epidemiology and evaluation methods, as well as

collaboration in economic evaluation projects. Her current areas of interest are the measurement of

“healthy workplace” performance and safety intervention effectiveness evaluation methodology. She is

the non-management co-chair of the Institute’s Joint Health & Safety Committee.

xiii
Harry S. Shannon

Harry Shannon is currently a Professor in the Department of Clinical Epidemiology Biostatistics and

Director of the Program in Occupational Health and Environmental Medicine at McMaster University,

Hamilton, Canada. He is also seconded to the Institute for Work & Health, Toronto, Canada as a Senior

Scientist.

Harry holds a B.A. in Mathematics from Oxford University, an M.Sc. from Birmingham University and

a Ph.D. in Applied Statistics at the University of London, U.K. He has authored over 75 peer-reviewed 

scientific papers, mainly in occupational health. 

Harry’s current research focus is on work-related injuries and musculoskeletal disorders, and psychosocial

conditions at work. Recent research includes studies of back pain in auto workers and upper extremity

disorders (“RSIs”) in newspaper workers. He has also studied the relationship between workplace

organizational factors and injury rates. Harry is a member of the Scientific Committee on Accident

Prevention (SCOAP) of the International Commission on Occupational Health (ICOH). He is on the

editorial board of Safety Science; and is a member of the NIOSH NORA group on the Social and Economic

Consequences of Occupational Illness and Injury.

xiv
1

1.1 What is a safety intervention?

A safety intervention is defined very simply as an

attempt to change how things are done in order

to improve safety. Within the workplace it could

be any new program, practice, or initiative

intended to improve safety (e.g., engineering

intervention, training program, administrative

procedure). 

Safety interventions occur at different levels of a

workplace safety system (Figure 1.1), including

the level of safety management and various

human and technical sub-system levels in the

organization that management can influence. An

additional level of the system in Figure 1.1, above

the organizational, pertains to the laws,

regulations, standards and programs put in place

by governments, industries, professional bodies,

and others. Examples of interventions at this

level include the Safe Communities Incentive

Program (Safe Communities Foundation,

Ontario, Canada), the Safety Achievers Bonus

Scheme (South Australian Workcover

Corporation) and small business insurance

pooling (CRAM, France). This guide does not

deal with interventions at the community level,

although some of the issues discussed are

applicable.

1.1 What is a safety intervention?

1.2 Effectiveness evaluation

1.3 Overview of the evaluation process and the guide

1.4 Other types of evaluation

Figure 1.1 Levels of intervention in the

workplace safety system

Introduction: Safety Intervention

Effectiveness Evaluation

Chapter 1
2

Introduction Chapter 1

1.2 Effectiveness evaluation

We are focusing here on effectiveness evaluation

(also known as outcome evaluation or

summative evaluation), which determines

whether a safety initiative has had the intended

effect. For example, such an evaluation might

answer the question, does the new incident

investigation process instituted three years ago

(for the purpose of decreasing injuries) actually

prevent injuries in subsequent years? This type

of evaluation is the “CHECK” portion of the

PLAN-DO-CHECK-ACT (PDCA) continuous

quality improvement cycle.4

Although injuries are often measured in an

effectiveness evaluation to determine whether

the initiative has had an effect or not, there are

two situations where this might not be the case.

One of them arises from injury outcome data that

is unreliable or invalid - (e.g., while evaluating

an initiative in a small workplace). In this case a

surrogate measure of safety could be used (e.g.,

a checklist of safety conditions), if shown to be

valid for the circumstances in which it will be

used. The other situation is where the program’s

explicit objective is not to decrease injury

incidence, but rather, some other objective such

as improve worker or management competence

or attitudes. 

However, if the purpose of the program is to

ultimately affect injury incidence by targeting

competence or attitudes, it would be beneficial

to include a measure of injuries or a valid

surrogate.

1.3 Overview of the evaluation

process and the guide 

Figure 1.2 provides an overview of the

effectiveness evaluation process. Much of the

activity in evaluation precedes the point where

the intervention or initiative is introduced.

Although evaluations can be done

retrospectively, appropriate data are typically

unavailable. The guidelines contained in this

guide assume that a safety need in the workplace

and the nature of the intervention have been

identified, but you are at a point prior to

introducing a new intervention in the workplace.

Even if this is not the case, and you have already

implemented your intervention, you should find

the guide relevant to the evaluation of your

intervention.

Chapter 2 identifies the decisions required before

people can work out the details of designing an

evaluation. They include the available resources,

time lines and, of course, the purpose of the

evaluation. A few of the broader methodological

issues, such as the use of qualitative and

quantitative methods and choice of outcomes,

are also introduced.

Chapters 3 and 4 introduce several evaluation

designs (i.e., methods of conducting evaluations

in conjunction with delivering an intervention).

These designs specify the groups of people or

workplace to be evaluated, as well as what will

be measured and when it will occur. 

Chapter 5 explains in more detail who to include

in the evaluation - a choice which affects the

generalizability of the evaluation results and the

types of statistical analyses to be used. 

The next two chapters (6 and 7) consider

quantitative (Chapter 6) and qualitative (Chapter

7) data collection methods. Quantitative

methods yield the numeric information

necessary to determine the size of an

intervention’s effect and its trustworthiness -

determined through statistical testing (Chapter

8). Qualitative methods yield conceptual

information which can inform the evaluation

design at the beginning, and the interpretation

of the results at the end. The guide ends with a

summary of the practice recommended in

previous chapters (Chapter 9). 

4 PDCA cycle mentioned in many references on quality improvement concepts. For example: Dennis P [1997] Quality, safety, and environment.

Milwaukee, Wisconsin: ASQC Quality Press.
Chapter 1 Introduction

3

1.4 Other types of evaluations

Other types of evaluation, besides effectiveness

evaluation, are useful in the process of improving

safety in the workplace. They will only be

described briefly here. A needs assessment can be

carried out to determine exactly what type of

intervention is required in a workplace. Analyses

of injury statistics, incident reports or employee

surveys, as well as interviews with key

workplace personnel (e.g., safety manager,

disability manager, union representative, etc.) can

identify particular safety issues. This determines

what type of intervention(s) should be chosen or

designed to address an identified need.

After choosing and introducing a new safety

initiative to a workplace, a process evaluation (also

known as a formative evaluation) can be used to

determine whether the new initiative is being

implemented as planned. It assesses to what

extent new processes have been put in place and

the reactions of people affected by the processes.

Furthermore, the refinement of a new initiative

and its implementation before its effectiveness

can be measured. If the process evaluation

determines that the initiative was not

implemented as planned, the time and trouble of

conducting an effectiveness evaluation might be

spared, or at least delayed until it becomes more

meaningful. 

Finally, economic analyses can be used to

evaluate workplace interventions, including costoutcome, cost-effectiveness and cost-benefit analyses.

They also depend on effectiveness information.

The first two analyses estimate the net cost of an

intervention (i.e., the cost of the intervention

Figure 1.2 Overview of the effectiveness evaluation process
4

Introduction Chapter 1

Table 1.1 Types of intervention evaluations

minus the monetary saving derived from the

intervention) relative to the amount of safety

improvement achieved. (Monetary savings

include reductions in workers’ compensation

premiums, medical costs, absenteeism, and

turnover, etc.) This yields a ratio such as net cost

per injury prevented. 

In a cost-benefit analysis, monetary values are

assigned to all costs and outcomes resulting from

an intervention, including health outcomes.

Furthermore, a net (monetized) benefit or cost of

the intervention is calculated. 

Drummond et al. [1994], Haddix et al. [1996] and

Gold et al. [1996] are useful introductions to

economic evaluations.
5

2.1 Introduction

2.2 Defining the scope of the evaluation

2.3 Who should be involved with the evaluation

2.3.1 Evaluation committee

2.3.2 Internal vs. external evaluators 

2.3.3 Technical or methodological expertise

2.4 Models to assist planning

2.4.1 Conceptual models

2.4.2 Program logic models

2.5 Quantitative vs. qualitative methods for collecting data

2.6 Choosing the evaluation design

2.6.1 Strength of evidence provided by different evaluation designs

2.6.2 Ethical considerations

2.7 Practical tips

2.7.1 Time management

2.7.2 Dealing with reaction to interim results

2.7.3 Intervention diary

2.7.4 Getting the cooperation of workplace parties

2.8 Summary

Planning Right from the Start

Chapter2
6

Planning Chapter 2

2.1 Introduction

One golden rule of intervention evaluation is that

the intervention and its evaluation should be

planned simultaneously. Decide on your

evaluation design and methods before the

intervention is introduced. If you do not, you

risk missing the only opportunity for collecting

important data before the intervention. 

This chapter gives some information about

organizing and carrying out an intervention

evaluation, including who to involve to oversee

the evaluation and how to use models to assist

with planning. It also highlights key issues to

consider during the planning stage. 

2.2 Defining the scope of the

evaluation

Some basic decisions are required before a

detailed evaluation strategy can be specified.

They should be done through a collaborative

process among those who will use the evaluation

results, and others either implementing the

intervention and evaluation project or funding

the evaluation. In a workplace setting, these

decisions should involve senior management.

The types of things to be determined at the outset

should include: 1) overall purpose of the

evaluation; 2) the main questions that the

evaluation should answer; 3) available resources

(financial, personnel, in-kind assistance); and 4)

the deadline for the evaluation results. These

have to be in place early on, since they will

influence the methodological deliberations. In

particular, the rationale for the evaluation will

influence the strength of the evidence sought.

For example, you might want a more rigorous

evaluation design if the result of the evaluation is

meant to inform a decision with larger resource

or policy implications.

2.3 Who should be involved with the

evaluation?

2.3.1 Evaluation committee

In all but the simplest evaluation, it is advisable

to assemble a committee to oversee the

evaluation. Ideally, this same group would also

interact with the evaluators in the selecting or

designing of the safety intervention. The larger

the potential resource and personnel impacts of

any conclusion drawn from the evaluation, the

greater is the need to have an evaluation

committee. The following factors can be

considered in deciding whether or not to set up

a committee.

People with different backgrounds and skill-sets

will be included in an evaluation committee and

any individual might play more than one role.

Key are those who will use, or could influence,

the use of the evaluation results. Their inclusion

will ensure the following: the evaluation will

address decision-makers’ concerns; the

evaluation and its results will be legitimized; and

communication of the evaluation results will be

initiated early in the evaluation process. You

need at least one person who can understand and

critique the methodological issues of both the

intervention and the evaluation. 

Also important is the expertise of those directly

affected by the intervention, who have special

insight into the reality of the workplace

conditions. Senior management and labor

representatives enhance the decision-making

capacity of the committee, as well as facilitate

required changes in workplace practices and

mobilize the cooperation of all involved.

Intervention skeptics are put to good use, as their

input will likely result in a more rigorous

evaluation. On the other hand, individuals

involved in either choosing or developing the

intervention should also be included, otherwise

they might be reluctant to accept any evidence

that their intervention is ineffective.
7

Chapter 2 Planning

There is a wide range of capacities in which

evaluation committees can function. At one

extreme, committee members can serve in a

relatively passive fashion, giving or denying

approval to what the core evaluation team

develops. At the other end of the spectrum

would be an action research model: all workplace

representatives and methodological experts

collaborate to formulate evaluation questions,

design the evaluation and interpret results. An

example of this model is the article by

Hugentobler et al. [1992]. The choice of where

to place the committee between the two extremes

involves weighing the complexity of the

intervention and how widespread the buy-in has

to be, as well as the time and resources available. 

2.3.2 Internal vs. external evaluators

From a scientific point of view, it is preferable

that an intervention is evaluated by an

independent party with no vested interest in

showing that the intervention is effective (or not

effective). In spite of all efforts to be openminded, it is simply human nature to put more

effort into finding and drawing conclusions from

information which confirms our expectations

than contradicts them. However, practitioners

often find they have to choose between carrying

out the evaluation themselves or having no

evaluation at all. Although the bias inherent in

an “in-house” evaluation is never entirely

removed, it can be diminished. This is achieved

by inviting others, especially those with opposing

views, to comment on analyses and reports of the

evaluation, and by being very explicit in advance

about what will be measured and regarded as

evidence of success or failure.

2.3.3 Technical or methodological expertise

It is quite possible that you might have to look

outside your own organization to tap into some

of the specialized skills required for certain

evaluations. Common areas requiring assistance

are questionnaire development and statistical

analysis. Consider contacting the local academic

institutions, for expertise in one of several

departments: biostatistics, occupational health &

safety, management, (social or occupational)

psychology, public health, education. Some

universities even have consulting services geared

to assisting community residents. Other means

of contacting experts would be through safety

research organizations, safety consultants or

safety professional organizations. In any case,

the rule is as before: involve these people early in

the evaluation.

Evaluation committee representation ideally includes:

• Stakeholders key to utilization and dissemination of results

• Key management representatives (e.g., relevant decision-maker)

• Key worker representatives (e.g., union representatives, opinion leaders, intervention participants)

• Evaluation expertise

• Diversity of disciplinary perspectives (e.g., engineering, safety, human resources, etc.)

• Diversity of workplace divisions/departments

• An intervention critic, as well as intervention proponents
8

Planning Chapter 2

2.4 Models to assist planning

Certain types of models can assist in planning all

but the simplest intervention and evaluation.

They diagrammatically depict the important

relationships among the workplace conditions,

interventions and outcomes, as well as identify

what should be measured in the evaluation. The

process of constructing models will often reveal

critical gaps in thinking and identify critical

issues. They also provide a means of generating

common understanding and communicating

among those involved in the intervention and

evaluation, as well as serving as an efficient aid

to communicating with others. 

One type of model is a conceptual model; another

is a program logic model. Both are somewhat

different and complementary: the conceptual

model tends to be more comprehensive in its

inclusion of factors which affect the safety

outcomes of interest and the program logic

model often includes more information on the

intervention itself. Conceptual models are used

by researchers in many disciplines, while

program logic models are used by program

evaluators - principally those evaluating social

or public service programs.

2.4.1 Conceptual models

A conceptual model typically uses arrows and

boxes to represent the causal relationships

(arrows) among important concepts (boxes)

relevant to an intervention. An example follows

(Figure 2.1).

The arrows indicate that structural management

commitment affects participative supervisory

practices, which in turn affect the workgroup’s

propensity for undertaking safety initiatives; and

these initiatives affect the likelihood of injuries.

The relationship represented by an arrow in a

model can be either positive or negative. We

expect a greater structural management

commitment will lead to more participative

supervisory practices - a positive relationship;

while greater workgroup propensity to

undertake safety initiatives would lead to fewer

injuries - a negative relationship. More complex

models show multiple relationships, involving

several arrows and boxes. Examples of more

complex models are included in an appendix to

this guide.

We recommend that a conceptual model relevant to

the intervention be developed6 while the

intervention is being chosen or designed. Ideally,

any model would be based as much as possible

on existing research and theory. You might adapt

an existing model to your own situation. The

conceptual model helps clarify what the

intervention hopes to change and the mechanism

by which that should happen. This clarification

could even reveal certain causal factors not yet

addressed by the intervention.

Structural management commitment

Participative supervisory practices

Workgroup propensity

to undertake safety initiatives

Injuries

Figure 2.1: An illustration of a simple

conceptual model 5

5 This model is based on some of the relationships reported in Simard M, Marchand A [1995]. A multilevel analysis of organizational factors related

to the taking of safety initiatives by work groups. Safety Sci 21:113-129.

6 For guidance in constructing conceptual models, see Earp and Ennett [1991].
9

Chapter 2 Planning

The conceptual model tells us what should be

measured in an evaluation. What we measure

using quantitative methods are known as

variables; i.e., attributes, properties or events

which can take on different values and

correspond to concepts in the model. Using the

conceptual model above, the numerical score

from supervisors completing questionnaires on

safety practices could be the variable

corresponding to the concept “participatory

supervisory practices”. 

Independent and dependent variables

As demonstrated, the conceptual model does not

describe the safety intervention itself, but rather,

depicts the variables expected to change during

an intervention. For example, the above model

might be applicable in an intervention where

structural management commitment was going

to be changed by establishing a joint

management-labor health-and-safety committee.

The variable being manipulated as part of the

intervention, i.e., presence or absence of a joint

health-and-safety committee in this case, is

known as the independent variable. 

In contrast, the variables affected by the

intervention, i.e., the variables corresponding to

the other three concepts in the model, are known

as dependent variables. These include the

variable(s) corresponding to the final outcome,

“injuries” in this case. They also include the

variables corresponding to the concepts which

mediate an intervention’s effect, e.g

“participatory supervisory practices” and

“workgroup propensity to take safety

initiatives”. The latter are known as mediating,

intervening or intermediate variables. 

Effect-modifying and confounding variables

Effect-modifying variables7 are sometimes

important to include in a conceptual model.

While these variables are not the focus of the

intervention, they often need to be considered

when data is collected and interpreted. An effectmodifying variable is one which modifies the size

and direction of the causal relationship between

two variables. For example, “participative

supervisory practices” might have a greater effect

on “workgroup propensity to take safety

initiatives” if the workgroup has more training in

safety or is younger. An effect modifying

variable is depicted by an arrow extending from

it to the relationship which it modifies, as Figure

2.2 shows.

Another type of variable to include in a

conceptual model is a confounding variable. This

is a variable which is related to the independent

variable (i.e. presence of intervention or not), as

well as the dependent variable of interest, but is

not a mediating variable. To build on the earlier

illustration, “industrial sector” could be a

confounding variable if one is looking at the

effect of changing “structural management

commitment” through the legislated introduction

of joint health-and-safety committees (see Figure

2.3). 

Suppose that you decided to evaluate the effect of

the legislation by comparing the injury rate of

organizations with established committees to

those without them. Suppose too, that the

industrial sectors with the higher injury rates are

more likely to have committees because of

greater inspector activity. If you were to then

compare injury rates of companies with

Figure 2.2: Depiction of an effectmodifying variable in a conceptual model

7 In some disciplines, such variables would be referred to as moderator variables.
10

Planning Chapter 2

committees (intervention group) versus those

without committees (control group), you would

find that the companies with the committees had

the higher injury rates. However, the result is

most likely due to the specific industrial sector,

rather than the intervention. Thus, a conclusion

that committees result in higher injury rates

would be inaccurate. You would form a different

conclusion if you took the sector into account in

the study design or analysis. To limit the

influence of confounding factors, take them into

account in your study design (preferable) or your

analysis.

2.4.2 Program logic models

Program logic models are highly regarded by

evaluators as a means of assisting evaluation

planning8

. They distinguish short-, intermediateand long-term outcome objectives. Figure 2.4

depicts a generic program logic model.

Implementation objectives are concerned with

the desired outputs of the intervention (e.g.,

provide training sessions). They are distinct from

outcome objectives, which are concerned with

the effects of the program. Continuing the

training example, a short-term objective could be

improved knowledge; an intermediate objective,

changed behavior; and a long-term objective,

decreased injuries. 

A program logic model, developed for a

particular safety intervention, could have more or

less boxes than shown in Figure 2.4, depending

on the number of intervention components and

objectives. Also, they could be linked in a

different pattern of arrows.

Like a conceptual model, the program logic

model gives insight into what should be

measured in an evaluation. Ideally, one selects a

means of measuring the achievement of each of

the objectives identified in the model. Figure 2.5

depicts an example of a program logic model for

a hypothetical ergonomic intervention.

Figure 2.3 Depiction of a confounding

variable in a conceptual model

Figure 2.4 Generic program logic model

8 Program logic models are explained by Rush and Ogborne [1991]
11

Chapter 2 Planning

A limitation of program logic models is that they

often do not depict additional variables, such as

confounding and effect-modifying variables. The

advantage is that they more explicitly indicate

the components of the intervention, and link

them with the intervention objectives. Both types

of models can be used to identify potential

unintended outcomes of the intervention. These

outcomes are not intended to result from the

intervention; but they nevertheless might. As

such, these outcomes can be difficult to

anticipate, but consideration of the models can

help. 

Using the models, one looks at the changes that

are supposed to happen following the

intervention. You then try to think about what

other effects could possibly result from the

changes. For example, an intervention to reduce

needle injuries by eliminating recapping prior to

disposal into containers might not only have the

intended effect of decreasing recapping injuries,

but also an unintended effect of increasing

disposal-related injuries if disposed into poorly

designed containers.

2.5 Quantitative vs. qualitative

methods for collecting evaluation

data

Tradeoffs are made in choosing which outcomes

to measure. These include consideration of the

quality of evidence required, available resources

and quality of data potentially available. In a

very complete effectiveness evaluation, you

collect pertinent data on all concepts represented

in the intervention models, some using

qualitative methods and others quantitative.

Quantitative methods involve measuring

indicators or variables related to the concepts in

Figure 2.5 Example of a program logic model for an ergonomic program
12

Planning Chapter 2

1) What is the strength of evidence required to address the purpose of the evaluation?

• What evaluation design will convince the decision-makers that the intervention has succeeded or failed?

2) Are there any ethical and legal considerations?

• Cannot assign people to a situation if one it is likely to be more harmful

• Some forms of data collection might require consent of individuals

3) What data collection and analysis is possible with the resources (financial, personnel, expertise) available? 

• Some forms of data collection are more expensive than others. 

4) Has the intervention been introduced already? If so, has some data collection already taken place?

• Circumstances may limit choices regarding the evaluation design

5) What is the time frame required and/or available for evaluation?

• Does demand for results preclude long-term measurement?

• What does preliminary research predict regarding the timing of the maximum program effect, as well

as any erosion of that effect

6) What does the conceptual model for the intervention suggest should be measured and when?

7) How does the organization of the workplace influence the design?

• Is randomization of workers/workplaces or the use of comparison groups possible? 

• Can an “intervention” group receive an intervention without other groups being aware? 

• How many workers/workplaces are available for the study?

8) Does the design offer sufficient statistical power?

Considerations in choosing an evaluation design

the models, such that they yield numerical data.

Qualitative methods, on the other hand, do not

yield numerical data and rely instead on

interviews, observation, and document analysis. 

To clearly demonstrate intervention effectiveness,

it is almost mandatory to use quantitative

techniques and measure an outcome variable

(e.g., injury rate). A demonstration of

statistically significant change or difference in

this variable (e.g., significant decrease in injury

rate) and its unambiguous attribution to the

presence of the intervention provides very good

evidence of intervention effectiveness. However,

when both qualitative and quantitative methods

are used in an evaluation, an especially rich

source of information is generated because the

two can provide a check and a complement for

each other. Whereas quantitative methods are

used to answer - “How big an effect did the

intervention have on the outcome(a) of interest?”

- and - “Was the effect statistically significant?”

- qualitative methods help answer - “How did

the intervention have that effect?” - and - “What

was the reaction of participants to the

intervention?”. Qualitative methods can also be

used at the earlier stage, when developing the

quantitative methods for the study, by answering

- “What would be important to measure when

determining the size of the effect of the

intervention?”

2.6 Choosing the evaluation design

Using the conceptual and/or program logic

models as a guide for measuring, you will then

choose an evaluation design. This is the general

protocol for taking measurements; i.e., from how

many group(s) of workers/workers will

measurements be taken and when will they be

taken? Choosing the design involves a

compromise among a number of considerations.

Some are summarized below and will be

discussed throughout the guide.
13

Chapter 2 Planning

2.6.1 Strength of evidence provided by

different evaluation designs

The goal of occupational safety intervention

research is to be able to say that a specific

intervention either enhanced, or did not enhance,

worker safety. The degree of confidence with

which you can legitimately draw this type of

conclusion depends on the strength of evidence

provided by the study. Usually, an experimental

design provides the strongest evidence of a causal

link between the intervention implementation

and observed effects. This design strength arises

from: 1) the use of a control group, which does not

participate in the intervention and is compared

with the group which does participate; and 2)

the assignment of people or workplaces to either

intervention and control groups through an

unbiased process (i.e., by randomization).

However, the logistical requirements of

experimental designs often cause them to be

unfeasible, especially for single, smaller worksites. In such cases, quasi-experimental designs,

should be considered. They represent a means

of compromising between the practical

restrictions of workplaces and the rigour required

for demonstrating intervention effectiveness.

They often include a control group, albeit one

created through a non-random process; and in

all cases, yield more information than a nonexperimental design. This last group of designs,

including the common before-and-after design, are

often necessary due to time and circumstances.

Although it provides weaker evidence, using a

before-and-after design is better than no

evaluation at all.

Table 2.1: Characteristics of different types of evaluation designs
14

Planning Chapter 2

2.6.2 Ethical considerations

Potential for harm vs. likelihood of benefit

Ethical considerations might be another reason

for not choosing to use an experimental design.

If there is preliminary evidence of a certain type

of intervention being beneficial or if it could be

presumed to be beneficial, you might not want to

plan an evaluation where some workers are

purposely put into a control group in which there

is a chance of great harm. For example, the

addition of machine guarding to a cutting

machine could promise to be very beneficial,

especially if there has been past severe injuries

that probably could have been prevented by

guarding. You might want to use only a beforeand-after design in this situation.

Individual consent

Different cultures have various views on what

types of research are ethically acceptable.

Modern Western societies tend to emphasize

individual autonomy and demand “fully

informed consent” from study subjects. For

example, in medical research, such consent is

required to enroll a patient in a study. 

The situation in North American workplaces is

somewhat different than in the medical field.

Management is considered to have certain

prerogatives, as well as legislated responsibilities

regarding safety, which allows it to make

decisions about what happens in the workplace.

Thus, employers can impose a new safety

intervention upon their work force, and people

might be assigned to an intervention group or

control group, without first seeking their consent.

This is less likely to occur in some European

countries, particularly Scandinavia, where more

worker participation exists in work-related

decisions. In addition, workplace research

carried out under the aegis of an academic or

federal research institution usually requires

approval by ethics committees, which will

certainly insist upon individual consent to obtain

data of a more personal nature (e.g., health

records, employee opinions).

2.7 Practical tips

2.7.1 Time management

The evaluator has to be careful about the time set

aside to properly conduct the evaluation. Often,

the need to implement the intervention and

resolve any unexpected problems can end up

monopolizing what hours are available for the

evaluation. The less obvious, but nevertheless

important, demands of consulting with the

evaluation committee and communicating with

workplace parties regarding the evaluation can

too easily fall by the wayside unless time is

allocated for them.

2.7.2 Dealing with reaction to interim results

Be prepared for the reaction by workers,

employers, etc. to interim results. If the results

are encouraging, the group designated as a

control may apply strong pressure to be allowed

to receive the intervention immediately and not

continue to incur possible risk until scientific

proof has been accumulated. Your evaluation

committee may come up with all sorts of interim

suggestions about ways to modify the

intervention, which could destroy the scientific

purity of the study. In the face of proposed

alterations to the intervention or evaluation

design, always keep in mind what effect the

proposed changes will have on your ability to

analyse, interpret and draw conclusions from

results. There is no easy single answer to these

dilemmas and the decision made will depend

partly on the importance of the evaluation

compared to the value of the change the

intervention is designed to produce. 

2.7.3 Intervention diary

We strongly recommend keeping a diary or logbook of the intervention and the evaluation, in

order to supplement formal data collection
15

Chapter 2 Planning

methods. It can be exceptionally valuable to look

back after the evaluation has revealed

unexpected results. The diary provides a

convenient place to record information about any

potential influences on the intervention outcomes

that were not taken into account by the

experimental design, including what is taking

place in the workplace - such as a change in

senior personnel or work processes. Evaluators

can also track decisions made over the course of

the evaluation which might not be documented

elsewhere. 

2.7.4 Getting cooperation of workplace

parties

A critical step in a successful intervention and

evaluation is obtaining the cooperation of all

involved. This includes the people in the

workplace participating in the intervention and

evaluation, their supervisors or managers, those

using the results of the evaluation and anybody

else interacting with the individuals or activities

just mentioned. Evaluation can be threatening. It

implies someone is checking, observing, and

questioning. It is vital to explain to those

involved what the evaluation is for, what will

happen to the information collected (particularly

if this is personal or confidential) and what will

be done with the results. 

Often, it is necessary to stress that the evaluation

aims to learn about and improve the intervention,

and not engage in criticizing or fault-finding. In

particular, individuals with a stake in the success

of the intervention will be sensitive, as will those

who chose or designed it, or invested time in

implementing it. Ongoing, repeated, clear, and,

ideally, interactive communications with all

involved is recommended. Communication can

help allay fears, reduce resistance to change,

increase acceptance of the evaluation results and

encourage adoption of the intervention, if shown

to be successful.

2.8 Summary

This chapter has introduced some of the initial

decisions and considerations that must be taken

into account in planning an evaluation. These

include the evaluators’ terms of reference and the

selection of an evaluation committee. It was also

shown how conceptual models and program

logic models can help identify what concepts

should be assessed for the purpose of an

evaluation. Such assessment can take place using

quantitative or qualitative methods. In addition,

there are a number of ethical considerations in

an evaluation. 

Once you have undertaken the broader decisions

outlined in this chapter, you will be ready to

choose the evaluation design. Options for

designs will be discussed further in Chapters 3

and 4.

• Decide objectives and scope of the evaluation.

• Involve all parties relevant to the intervention (expertise, influence, etc.) in planning and at subsequent stages

of the evaluation.

• Make a conceptual model relevant to the intervention, identifying concepts which must be measured or

accounted for in the design.

• Make a program logic model.

• Start designing the evaluation, considering several aspects.

• Consider using a quasi-experimental or experimental design, if permitted by feasibility and ethical

considerations.

• Keep an intervention diary.

Key points of Chapter 2
16

Planning Chapter 2
17

3.1 Introduction

3.2 Design terminology

3.3 Non-experimental evaluation designs

3.4 Before-and-after design

3.5 Threats to internal validity of before-and-after designs

3.5.1 History threat

3.5.2 Instrumentation/reporting threat

3.5.3 Regression-to-the-mean threat

3.5.4 Testing threat

3.5.5 Placebo and Hawthorne threats

3.5.6 Maturation threat

3.5.7 Dropout threat

3.6 Summary

Before-and-after design:

A simple evaluation design

Chapter3
18

Before-and-after Design Chapter 3

3.1 Introduction

Chapters 3 and 4 will discuss three basic types

of evaluation designs: non-experimental; quasiexperimental; and experimental.9 These designs

differ in the strength of evidence they provide

for intervention effectiveness. We can be more

confident in a result from an evaluation based on

an experimental or quasi-experimental design

than with a non-experimental design; but often

we have no choice. We either have to use a nonexperimental design or not attempt any

evaluation. In this case, we advise that a nonexperimental design is better than none at all. 

Chapter 3 therefore focuses on the before-and-after

design, a type of non-experimental design

commonly used in safety studies. We outline

some of the reasons the before-and-after design

must be used with caution. These are called

threats to internal validity; i.e., circumstances

which threaten our ability to correctly infer

whether or not the intervention had the desired

effect. Chapter 4 will cover quasi-experimental

and experimental designs.

3.2 Design terminology

In design terminology, “before” refers to a

measurement being made before an intervention

is introduced to a group and “after” refers to a

measurement being made after its introduction.

Equivalent terms for “before” and “after” are

“pre” and “post”. 

3.3 Non-experimental designs

The before-and-after design is the most

important non-experimental design for our

purposes, since it is a reasonable option for an

evaluation. Although it suffers from many

threats to internal validity, it can, in many cases,

provide preliminary evidence for intervention

effectiveness, especially when supplemented

with complementary information. We will

consider it in detail in Sections 3.4 and 3.5. There

are also two other types of non-experimental

designs: after-only and after-only-with-a-nonrandomized-control-group. As implied,

measurement is made only after the

intervention’s introduction in both of these

designs and, hence, they are less desirable. 

An example of an after-only design is where you

measure safety knowledge in a test only after you

train a work group. The weakness of this

approach is that you cannot be sure whether the

test score would have been any different without

training. Even if the average score after training

was 90%, the training might actually have been

ineffective, since the group might also have

scored 90% on the test if it had been given before

the training. Thus, the only acceptable use for

this type of design is to ascertain if a certain

standard has been met. It is not useful for

effectiveness evaluation.

An example of the after-only-with-a-nonrandomized-control-group design is a case where

you measure knowledge in one group following

training, and also measure it in another group

which did not have the training. If the score is

higher in the first group than in the second, for

example, 90% compared with 80%, you might be

tempted to think that the training had been

effective. However, once again, you cannot tell if

the training had any impact, because you do not

know what the “before” values would have been.

If they had been 90% and 80% respectively, your

conclusion regarding program effectiveness

would have been wrong. Thus, the after-onlywith-non-randomized-control-group design is

also not useful for effectiveness evaluation.

9 We follow the classification described by Cook and Campbell [1979] and Cook et al. [1990].
19

Chapter 3 Before-and-after Design

3.4 Before-and-after design

The before-and-after design offers better

evidence about intervention effectiveness than

the other non-experimental designs just

discussed. Consider our example of training.

Suppose a group had been given a test of

knowledge in the morning and scored 50%, and

following a day of training, the group repeated

the same test and scored 80%. [We illustrate this

in the above figure by each “O” representing a

measurement (in this case, the test), and the “X”

representing the introduction of the intervention

(training).] In this situation, the evidence would

be strong that the training caused the increase in

test score. Another way of saying this is that the

evidence of causality would be strong. Besides

the training, little else over the course of the day

could have caused the observed increase in

knowledge (provided of course that we do not

use an identical test on the two occasions and

give the group the answers in the meantime).

The before-and-after design is most useful in

demonstrating the immediate impacts of shortterm programs. It is less useful for evaluating

longer term interventions. This is because over

the course of a longer period of time, more

circumstances can arise that may obscure the

effects of an intervention. These circumstances

are collectively called threats to internal validity. 

3.5 Threats to internal validity of

before-and-after designs

Threats to internal validity are possible alternative

explanations for observed evaluation results. The

more threats to internal validity, the less

confident we are that the results are actually due

to the intervention. A good evaluation identifies

the possible threats to its internal validity and

considers them one-by-one as to the degree of

threat they pose. 

One way to minimize the threats to validity is to

consider other data or theory. In doing so, you

might be able to render a particular threat to

validity highly unlikely. Or, you might be able to

show that it poses a minimal threat and thus does

not change the conclusions of the evaluation.

Some of the later examples illustrate this

approach.

The ideal way of dealing with internal validity

threats is by using a quasi-experimental or

experimental design. Chapter 4 will show that

you can eliminate most of the threats we are

about to discuss by including a good “nonrandomized control group” in your evaluation

design. However, in the following we will

assume that it has only been possible to

undertake a before- and-after design. Our

suggestions for dealing with threats to internal

validity are made with this limitation in mind.

O X O
20

Before-and-after Design Chapter 3

History Some other influential event(s), which could affect the outcome, occurs during the 

intervention

Instrumentation/Reporting Validity of measurement method changes over course of the intervention

Regression-to-the-mean Change in outcome measure might be explained by a group with a one-time extreme value 

naturally changing towards a normal value

Testing Taking measurement (e.g. test) could have an effect on the outcome

Placebo Intervention could have a non-specific effect on the outcome, independent of the key 

intervention component

Hawthorne Involvement of outsiders could have an effect on the outcome, independent of the key 

intervention component

Maturation Intervention group develops in ways independent of the intervention (e.g. aging, increase 

experience, etc.), possibly affecting the outcome

Dropout The overall characteristics of the intervention group change due to some participants 

dropping out, possibly affecting the outcome

Threat to internal validity Description of threat

Table 3.1:Threats to internal validity

3.5.1 History threat

A “history threat” occurs when one or more

events, which are not part of the intervention but

could affect the outcome, takes place between the

“before” and “after” measurements. Common

history threats include changes in the following:

management personnel; work processes,

structure or pace; legislation; and managementlabor relations. Clearly, the longer the time

between the “before” and “after” measurements,

the more opportunity is there for an extraneous,

interfering event to happen. 

There are two history threats in the

accompanying example (opposite), one from

outside the company and the other from inside.

Either the community campaign or the human

resource initiatives - or both - are alternative

reasons for the observed decrease in injury rate.

You are trying to evaluate a new ergonomic

intervention for nurses in a hospital. An

educational program about back health and

lifting techniques was provided, a program

of voluntary stretches introduced and lifting

equipment purchased. It was found that the

injury rate for the two years before the

intervention was 4.4 lost-time back injuries

per 100,000 paid hours and for the two years

following it was 3.0. Thus, you conclude that

the ergonomic intervention has been effective. 

But what if one month after the education

program, a government ministry launched a

year-long public awareness campaign aimed

at reducing back injury? And, what if the

president of the hospital was replaced two

months after the in-house ergonomic

program and her replacement introduced

human resource initiatives to improve

communication among staff? This would

make you less confident about concluding

that it was the intervention alone that made

the difference in back injuries.

Example of a history threat
21

Chapter 3 Before-and-after Design

How to deal with history threats

The opportunities for history threats to arise in

safety intervention evaluations are considerable

because of the complex nature of the workplace

and its environment. Careful consideration

should be given to the events which could affect

the safety outcome of interest. Earlier, an

intervention diary was recommended as a means

of keeping track of such events throughout the

intervention and evaluation. Interviews with key

personnel, a form of qualitative investigation, can

also identify significant events that have taken

place. [Qualitative methods are discussed in

Chapter 7]. Even if none have occurred in the

broader environment or the workplace itself, it

is important to be able to confidently state this

in the report of findings from a before-and-after

design. 

If you do identify a history threat, try to estimate

how large an effect the threat would likely have

had. The following example illustrates how you

can use other data to estimate these possible

effects.

Consider the preceding example of the

hospital ergonomic program which appeared

to have decreased back injury rates. To

reduce the threat of the community

campaign, you could try to obtain statistics

on changes in back injury rates for other

hospitals in the same community. If the injury

rate in the other hospitals had remained

constant or increased, you could conclude

that changes in your hospital (i.e., either the

ergonomic intervention or human resource

(HR) initiatives) had an effect on injury rates

beyond any effect of the community

education program.

As far as considering the effect that the HR

initiatives might have had on injury rates, you

could look at other HR-related outcomes, e.g.,

non-back related absenteeism, non-back

related health care claims or turnover. You

reason that if the HR initiatives were

powerful enough to have an effect on injury

rates, then they should also affect other

employee-related health indicators. If these

other outcomes show little change, you could

be more confident that the observed decrease

in injury rates was due to the ergonomic

program alone and not the president’s

initiatives. 

Example of dealing with a history threat
22

Before-and-after Design Chapter 3

3.5.2 Instrumentation/reporting threat

An instrumentation threat to validity occurs

whenever the method of measuring safety

outcome changes between the “before” and

“after” measurements. There are many ways this

could happen, depending on the type of outcome

measured, as the following examples illustrate

(Exhibit 3.1). 

An instrumentation threat of special concern in

safety evaluations using injury statistics is any

change in injury reporting over the course of the

evaluation. Sometimes, this arises simply

through changes in administrative policies or

procedures: e.g., the definition for an injury’s

recordability changes or the recognition of an

injury as work-related changes. A particularly

tricky situation arises when the intervention itself

affects the reporting of incidents, as the following

examples portray (Exhibit 3.2).

1) You are evaluating a new, redesigned

workstation by taking electromyographic

measurements of muscle activity in

workers using their old workstations and

then again in the same workers with the

new workstations. You did not realize

that at the time the measurements were

taken at the old workstations, the

equipment was malfunctioning, leading

to an underestimate of the true values.

2) You give a multiple choice pre-test of

knowledge with four possible choices:

unlikely, somewhat unlikely, somewhat

likely and likely. Afterwards, someone

comments to you that they had a hard

time choosing among the four choices and

would have liked a “don’t know” option.

In the post-test you decide to give five

possible choices, the four above, plus

“don’t know”.

3) You ask workers to fill out a safety climate

questionnaire before and after the

introduction of a joint health and safety

committee in the plant to evaluate the

committee’s effectiveness in changing the

safety climate. The first time, employees

filled out the questionnaire on their own

time; the second time, they were given

time off during the day to complete it.

Exhibit 3.1 Examples of instrumentation

threats

1) You are evaluating the effect of

undergoing a voluntary safety audit on

the work-site by looking at injury

statistics before and after introduction of

the audit. You realize, however, that the

audit includes a section on data collection

procedures which could affect the

reporting of incidents on the work-site.

The increased reporting could cancel out

any reduction in actual injuries. Thus,

any change in injury statistics following

the audit, might be due to the new

reporting process alone, and not to true

change in the injury rate.

2) A mandatory experience rating program

was introduced by the government. This

gives companies financial incentives and

penalties based on past injury statistics.

Following the introduction of the

program, it was found that lost-time

injury frequency for the jurisdiction had

declined. Critics of the program cite

anecdotal evidence of workers with

serious injuries being pressured to accept

modified work. No one can be certain

that the decline in injury frequency results

from enhanced injury prevention or from

simply a suppression of reporting.

Exhibit 3.2 Examples of reporting threats

arising from intervention 
23

Chapter 3 Before-and-after Design

Dealing with instrumentation and reporting

threats

The best way to deal with most instrumentation

threats is to avoid them in the first place. Keep

“before” and “after” measurement methods

constant. Make sure all measuring equipment is

functioning properly. Give questionnaires in the

same format and under the same conditions for

all measurements. Keep processes for generating

and collecting injury statistics constant. 

In the cases where the intervention itself might

have affected the reporting of injuries, especially

minor injuries, take a close look at the ratio of

major-to-minor injuries. The greater the

suppression of reporting, the higher this ratio will

be, because minor injuries are easier to not report

than major injuries. If the ratio is constant, then

the likelihood of an instrumentation threat is

reduced. You can also interview key informants

to learn if the intervention affected reporting.

3.5.3 Regression-to-the-mean threat

Regression-to-the-mean is an issue when the basis

for choosing the intervention group is a greater

apparent need for the intervention (e.g., higher

injury rates). This situation is not unusual as the

following examples illustrate (Exhibit 3.3).

An alternative explanation for the apparent

success of the safety initiatives is “regression- tothe-mean”. This concept can be understood as

follows. From year-to-year a group’s or

company’s injury rates will fluctuate - sometimes

they will be higher and sometimes lower. Any

group with a lower than usual injury rate in any

given year is therefore more likely to have their

rates increase than decrease in the following year,

assuming workplace conditions do not change.

Similarly, the odds are that any group with a

higher than usual injury rate in any given year is

more likely to have their rates decrease than

increase in the subsequent year. Thus, if the

intervention includes only groups with high

injury rates, a part of any decrease observed may

have nothing to do with the intervention itself.

Rather, the rate is simply moving closer to the

average rate.

Exhibit 3.3 Examples of regression-to-themean threats

1) Division A of the manufacturing company

had an unusually high rate of slip and fall

injuries last year. The president is

concerned and an enhanced inspection

schedule is therefore implemented. Rates

are lower the following year and so it

appears that the intervention was

successful.

2) The government labor ministry has

decided to implement a new educational

initiative with companies whose injury

rate in the previous year was twice as

high as the average for their industrial

sector. Personal contact was made with

officials of those companies, at which time

penalty-free on-site inspection and advice

was offered. The group of companies

had, on average, a lower injury rate the

following year. Thus, it appears that the

ministry program was successful.
24

Before-and-after Design Chapter 3

Dealing with regression-to-the-mean threats

There is nothing that can be done to deal with a

regression-to-the mean threat if you have a single

measure of frequency or rate before the

intervention and one after, for a single workplace.

However, with historical data, you can see

whether the before measurement is typical of

recent data or if it is an outlier. If it is the latter,

then regression-to-the mean does threaten the

validity of the conclusions and you might want

instead to use more of the historical data to

calculate the pre-intervention frequency or rate.

Hauer [1980, 1986, 1992] has developed statistical

approaches that correct for this phenomenon in

data from multiple work-sites. However, an

alternative approach would be a quasiexperimental or experimental design, where

some high injury groups receive the intervention

and others are kept under control conditions for

comparative purposes.

3.5.4 Testing threat

A testing threat to internal validity is a concern

when the act of taking the before measurement

might itself affect the safety outcome used to

evaluate the intervention. This threat is only an

issue for such outcomes as worker safety

knowledge, attitudes or practices. Any of these

could be affected by the act of taking initial

measurements by methods involving

questionnaires, interviews or observations. This

contrasts with injury outcomes which can usually

be measured without interacting with workers.

Dealing with the testing threat

If you always plan to give a pre-test before giving

the intervention, you do not really need to know

whether any observed effect was due to the pretest, the intervention, or the combination of both.

However, you then must continue to include the

pre-test as part of the intervention package.

Removing the pre-test risks decreasing the

overall effect of the intervention. If you want to

do away with the pre-test, you should at first

continue to include a post-test. You can then

check to see whether the post-test results are

affected by the pre-test’s removal. If not, and if

the groups with which you are intervening are

similar over time (and so similar pre-test scores

can be assumed), then you can conclude that a

testing effect was unlikely. However, a truly

definitive investigation of a testing effect requires

a quasi-experimental or experimental design.

You want to evaluate a training intervention designed to increase worker participation in plant safety.

You use a questionnaire to assess pre-intervention worker attitudes, beliefs and practices concerning

participation. You administer a second, post-intervention questionnaire after a three month program

of worker and supervisor training. Comparison of the questionnaire results show a significant change

in scores, indicating that participation has increased.

Upon reflection you are not really sure what accounts for the improvement in the score. You reason

that it could be any of the following: a) an effect of the training program alone; b) an effect of having

awareness raised by completing the first questionnaire; or c) a combined effect of completing the

questionnaire and then experiencing training. Either of the latter two possibilities involves a testing

threat to the internal validity of the evaluation.

Example of a testing threat
25

Chapter 3 Before-and-after Design

3.5.5 Placebo and Hawthorne threats

The “placebo effect” is a concept from clinical

studies of medical treatments. It has been

observed that a percentage of the study subjects

treated with a placebo (i.e., an inactive

substance), instead of a medical treatment, will

show an improvement of symptoms beyond that

expected of the normal course of their medical

condition. It seems that the placebo operates

through a psychological mechanism which

results in an alleviation of symptoms. The

patients believe that the treatment will be

successful and this has an effect in itself on the

outcome.

The “Hawthorne effect”10 usually refers to an

effect of the involvement of researchers or other

outsiders upon the measured outcome. This term

arose from a famous study of factory workers at

Western Electric’s Hawthorne Works in the 1920s.

A subset of workers was moved to a different

section of the factory, their working conditions

manipulated and the effect of this on their

productivity observed. It turned out that

workers were more productive under any of the 

work conditions tried - even uncomfortable one

like low lighting conditions. It is believed that

the effect of the new psychosocial working

conditions (i.e., increased involvement of

workers) in the experimental situation actually

overshadowed any effect of the changes in the

physical environment.

Dealing with Hawthorne or placebo effects

requires somehow “separating” them from the

effect of changing an injury risk factor as part of

the intervention. In the example above, the effect

of the consultant (and that of taking observations)

was separated from the effect of providing

feedback by having the consultant take baseline

measurements prior to starting the feedback. 

Due to an increasing prevalence of “repetitive

strain injury” in a telecommunications firm,

the management agreed to purchase new

keyboards for one division. A survey of

employee upper extremity symptoms was

conducted the week before the keyboards

were introduced and then three weeks

afterwards. Everyone was pleased to find a

significant decrease in reported symptoms

between the “before” and “after”

measurements. Management was on the

verge of purchasing the same keyboards for a

second division, but there was concern about

a “placebo effect” of the new keyboard. 

Example of a placebo threat

A work-site decides to implement and

evaluate a new training program focused on

changing safety practices by providing

feedback to employees. A consultant

examines injury records and, with the help of

workers and supervisors, develops a checklist

of safety practices. The list will be used by

the consultant to observe the work force and

provide feedback to the employees about

their practices. The consultant realizes that

his presence (and the taking of observations)

could make workers change their normal

behavior. To avoid this potential Hawthorne

effect, he makes baseline observations on a

daily basis until his presence seems to no

longer create a reaction and the observations

become constant.

Example of a Hawthorne threat and one

way to deal with it.

10 Some discourage the continued use of this term. See Wickström G, Bendix T [2000]. The “Hawthorne effect” - what did the original Hawthorne

studies actually show? Scan J Work Environ Health 26:363-367
26

Before-and-after Design Chapter 3

3.5.6 Maturation threat

A maturation threat to internal validity occurs

when the apparent change in safety outcome

could be due more to the intervention group

changing naturally (i.e., employees growing

older, or becoming more knowledgeable, and

more experienced) rather than to the intervention

itself. 

Dealing with maturation threats

In the example above, we need to consider aging

of the work force as a maturation threat. A

statistician might eliminate this maturation threat

by using appropriate statistical techniques in the

analysis. With such a correction in the above

example, we might find that the program actually

had either no effect or even a positive effect,

instead of the apparent detrimental effect.

3.5.7 Dropout threat

The dropout threat to internal validity arises

when enough people drop out of the study to

alter the characteristics of the intervention group.

Furthermore, these characteristics are statistically

related to the safety outcome of interest. This

would not matter if you could still measure the

safety outcome on all people who started the

program. For instance, some individuals might

drop out of a company back belt program. Yet, if

they continue to work for the company, you

could still evaluate the intervention if the

company injury rate data for the entire

intervention group is available. Not surprisingly,

safety outcome data on drop-outs is not always

accessible, as the following example illustrates.

A shipping company instituted annual

medical screening for their dock-workers in

order to identify and treat musculoskeletal

problems early. Injury statistics after four

years of the program indicated that the

incidence of injuries remained about the

same, but the length of time off work per

injury had been increased. It appeared that

the program had been detrimental. But an

occupational health nurse pointed out that

there is a tendency for older workers to return

to work more slowly than younger workers,

following an injury. Because there had been

few new hires at the company, this

maturation threat was a real possibility.

Example of a maturation threat 

An evaluation of an intervention to reduce

farmer injuries takes “before” and “after”

measurements using a questionnaire. The

questionnaire includes questions about

injuries requiring hospital treatment

experienced over the past year.

Unfortunately, over the course of the

intervention, a large number of farmers

withdraw and do not fill out the

questionnaire again. Thus, “after”

measurements are not possible for a large

percentage of participants.

You find that the average self-reported injury

rate for the group decreased and so it appears

that the intervention had an effect. But you

can not be sure whether this was actually due

to the intervention or that those with higher

injury rates dropped out of the study earlier.

Example of a dropout threat
27

Chapter 3 Before-and-after Design

Dealing with a dropout effect

If you have access to final outcome data for the

individuals or groups who dropped out of the

intervention, be sure to include their data with

that of the others assigned to the intervention at

the start of the study (as long as it does not

contravene the conditions described in their

consent form). This estimate of intervention

effect will give a minimal, conservative estimate

of the program’s potential since not everyone was

exposed to the program for the full length of time. 

If you do not have access to final outcome

measures for intervention dropouts, an important

thing to do is compare the “before” measurement

of dropouts, as well as their other characteristic

(e.g., age), with those who continued with the

intervention. If those who continued and those

who dropped out are similar in these

measurements, then the threat of dropout on the

outcome is reduced. You can assume that if the

dropouts and others were the same before the

intervention, they would also be similar

afterwards, with the exception of having

completed the intervention. If the “before”

measurements or other characteristics of the

dropouts are different, then the threat of dropout

persists. You could confine the estimate of the

program’s effectiveness to those individuals who

participated for the entire length of the program.

However, the results would not be generalizable

to the entire target population and likely

overestimate the program’s effectiveness for that

population.

3.6 Summary

This chapter focused on the before-and-after

design, which is considered to be a type of nonexperimental design. A before-and-after

evaluation design was shown to suffer from

several threats to internal validity: history,

instrumentation, regression-to-the-mean, testing,

placebo, Hawthorne, maturation and dropout.

Fortunately, as the illustrations showed, these

threats to internal validity can be handled to

some extent by additional data collection or

analysis. 

We also showed the inherent vulnerability of a

before-and-after design to internal validity

threats, especially for long-term evaluation

periods. The longer your intervention and

evaluation, the more you will want to consider a

quasi-experimental design as an alternative. We

discuss both quasi-experimental and

experimental evaluation designs in the next

chapter.
28

Before-and-after Design Chapter 3

• If you have no choice but to use a before-and-after design, try to eliminate the threats to internal

validity.

• Identify other changes in the workplace or community that could have an effect on the outcome

(history threats) and estimate their possible effect.

• Ensure that before and after measurements are carried out using the same methodology (to avoid

instrumentation or reporting threats).

• Avoid using high-injury rate groups, or other such extreme groups, as the intervention group in a

before-and-after study (to avoid regression-to-the-mean threats).

• Allow for the fact that taking a test can have an effect of its own (testing threat).

• Identify possible placebo or Hawthorne threats and try to minimize them.

• Identify any natural changes in the population over time which could obscure the effect of the

intervention (maturation threat), and possibly correct for their effect during the statistical analysis.

• Identify the effects of intervention participants dropping out and allow for this in the analysis.

Key points of Chapter 3
29

Quasi-experimental and

experimental designs:

more powerful evaluation designs

Chapter4

4.1 Introduction

4.2 Quasi-experimental designs

4.2.1 Strategy #1: Add a control group

4.2.2 Strategy #2: Take more measurements (time series designs)

4.2.3 Strategy #3: Stagger the introduction of the intervention

4.2.4 Strategy #4: Reverse the intervention

4.2.5 Strategy #5: Measure multiple outcomes

4.3 Experimental designs

4.3.1 Experimental designs with “before” and “after” measurements

4.3.2 Experimental designs with “after”-only measurements

4.4 Threats to internal validity in designs with control groups

4.4.1 Selection threat

4.4.2 Selection interaction threats

4.4.3 Diffusion or contamination threat

4.4.4 Rivalry or resentment threats

4.5 Summary
4.1 Introduction

In Chapter 3 we described the simplest type of

evaluation design for intervention effectiveness

evaluation, the before-and-after or pre-post

design. We showed how its strength is inherently

limited by several threats to internal validity. 

In this chapter, we discuss several types of quasiexperimental and experimental designs. All offer

some advantages over the simple before-andafter design, because some of the threats to

internal validity are eliminated. In the first

section we show how a quasi-experimental

design evolves from the addition of one or more

design elements to a before-and-after design.

After this, we describe experimental designs.

Although the latter offer the greatest strength of

evidence, quasi-experimental designs are often

more feasible in workplace situations. We close

this chapter with the discussion of various threats

to internal validity that arise with a control or

comparison group.

4.2 Quasi-experimental designs

There are five basic strategies to improving upon

a before-and-after design. This section describes

common approaches to adopting one or more of

these strategies.

4.2.1 Strategy #1: Add a control group (e.g.,

pre-post with non-randomized control)

The pre-post with non-randomized control design

mimics a simple experimental design. Like the

experimental design, there is at least one group

which receives the intervention (intervention

group) and one group which does not (control

group)11. The difference lies in the way

participants are assigned to groups for the

purpose of intervention implementation and

evaluation. In an experiment participants are

randomly assigned;12 in quasi-experimental

designs, they are not. Often assignment of

participants to a group is predetermined by the

work organization. For example, you might

deliver an intervention to one company division.

Another division, which is similar, acts as a nonrandomized control group by not receiving the

intervention. In the example below, the

assignment of reindeer herders to intervention

and control groups was determined by

geographical location. 

Quasi-experimental and Experimental Designs Chapter 4

30

Design strategies which change a before-andafter design into a quasi-experimental design

Strategy 1: add a control group

Strategy 2: take more measurements before

and after the intervention

implementation 

Strategy 3: stagger the introduction of the

intervention among groups

Strategy 4: add a reversal of the intervention

Strategy 5: use additional outcome measures

11 The terminology varies regarding the use of the term “control group”. Some use it only in the context of experimental designs, in which the

intervention and control groups are formed through randomization. Others, including ourselves, also use the term control group in the context

of quasi-experimental designs, in which groups are formed through a non-random process. In this case, the quasi-experimental control group

is referred to as a “non-randomized control group”. “Comparison group” is sometimes a synonym for “control group”, but in other cases is

reserved to describe the non-intervention group in a quasi-experimental design.

12 Random assignment of participants to groups is discussed in Section 5.4.
Advantages of the “pre-post with nonrandomized control group” design

By adding a non-randomized control group to

the simple before-and-after design, you

automatically reduce some of the threats to

internal validity discussed in Chapter 3. In

particular, interference by external circumstances

(i.e., history effects) is reduced, because they will

often apply to both the control group and the

intervention group. It therefore allows a

separation of the effect of the intervention from

that of other circumstances. The following

example illustrates this. The above example demonstrates that it is

possible to conclude that an intervention is

ineffective, even though fewer accidents are seen

after the intervention. The control group showed

the evaluators how much change to expect in the

absence of the intervention. These changes were

likely due to history, and possibly, testing and

Hawthorne effects, according to the original

report by Pekkarinen et al.13 Thus, we see how

the presence of the control group allowed one to

examine the intervention effect, free from the

influence of internal validity threats.

On the other hand, a new threat to validity -

selection effects - arises from using a nonrandomized control group. This threat occurs

when the intervention and control groups differ

with respect to the characteristics of group

participants and these differences influence the

measures used to determine an intervention

effect. Selection effects will be discussed further

at the end of the chapter.

Chapter 4 Quasi-experimental and Experimental Designs

31

Example of a pre-post with randomized

control group design

Due to the high rate of injuries among

reindeer herders, preventive measures were

developed. In intervention group A, letters

describing possible preventive measures were

sent to district leaders and contacts, who were

asked to pass on the information to herders in

their district. In intervention group B,

occupational health personnel trained in

prevention measures passed on information

during medical examinations. There was also

a control group C, which received no

intervention. Pre-post statistics for the three

groups are shown below.

Statistical analysis confirmed that the groups

did not differ in terms of a decrease in

accident rate. The authors had to conclude

that the intervention efforts were ineffective.

13 Data from Pekkarinen et al. [1994] with permission of the Arctic Institute of North America.

Number of accidents/working days for

reindeer herder groups13
4.2.2 Strategy #2: take more measurements

(time series designs)

A simple time series design differs from the simple

before-and-after design by taking additional

measurements before and after the intervention.

A baseline time trend is first established by taking

several outcome measurements before

implementing the intervention. Similarly, in

order to establish a second time trend, several of

the same measurements are made after

introducing the intervention. If the intervention

is effective, we expect to find a difference in

outcome measures between the two time trends. 

Advantages of simple time series design

Figure 4.1 illustrates how much easier it is to

interpret the results of a time series evaluation

design than a simple before-and-after design. In

the first panel we see that there has been a drop

in our safety measure from the period before the

intervention to the one afterwards. As discussed

in Chapter 3, several possible alternative

explanations for this come to mind, e.g., history,

maturation, instrumentation or Hawthorne

effects. By adding measurements, as shown in

the second panel, we can reduce the likelihood

of some of these alternative explanations. 

The maturation threat is eliminated because we

observe that the change between the baseline

time trend and the second time trend is abrupt.

In contrast, changes due to maturation, such as

increasing age or experience, are more gradual.

Regression-to-the-mean or testing effects have

also been eliminated as possible threats because

we can see that safety outcomes are repeatedly

high before and repeatedly low afterwards.

Placebo and Hawthorne effects are less likely

explanations because they tend not to be

sustained once people have adapted to a change

in their conditions. The threat of a history effect

is somewhat lessened because the window of

opportunity for a coincidental event is narrowed

by the more frequent measures taken. Dropout

and instrumentation both remain as threats,

without consideration of additional information.

How many measurements are needed for a

time series design?

The number of measurements you need for a

time series design depends on the amount of

random fluctuation (noise) that may occur in the

outcome being measured and how much of an

impact the intervention is expected to have.

Somewhere between 6 to 15 measurements to

establish a baseline and the same number again

to establish the trend afterwards are typically

required.14

Because of the necessity for many measurements,

Quasi-experimental and Experimental Designs Chapter 4

32

Figure 4.1 Comparison of before-and-after

and time series designs

Safety outcome

Time

Time

Before-and-after design

Simple time series design

Intervention commences

Intervention commences

Safety outcome

14 Several workplace examples can be found in Komaki and Jensen [1986].
the time series design is suitable for only some

situations. For example, a time series design,

using injury rate as the outcome measure would

likely not be suitable for a small workplace. It

simply takes too long - a year or more - for a small

workplace to establish a reliable injury rate.

On the other hand, the design could be quite

suitable in a group of small workplaces, a bigger

workplace, or if observed work-site conditions

were measured instead of injury rate. These

situations permit more frequent and reliable

measurement.

Even when it is not possible to take as many

measurements as are needed for a time series

analysis, taking additional measurements over

time is still a good idea. It gives you a better

sense of the pattern of variability over time and

whether the last “before” measurement is typical

of the ones preceding and the first “after”

measurement is typical of the ones following.

You are better informed of potential threats to

internal validity and the sustainability of the

intervention’s effect. It may allow you to better

estimate the effect of the intervention more

accurately by pooling data.

Multiple time series designs

Even better than using basic strategy #1 or #2

alone, you can strengthen the before-and- after

design even more, by combining both approaches

(adding a control group and taking more

measurements). 

4.2.3 Strategy #3: Stagger the introduction of

the intervention (e.g., multiple baseline

design across groups)

A special type of multiple time series design is

known as “multiple baseline design across

groups”. With this design, all groups eventually

receive the intervention, but at different times.

As a result, all groups also serve as a comparison

group to each other.

Advantages of the multiple baseline across

groups design

The advantage of the multiple baseline across

groups design is that it markedly reduces the

threat of history effects. When an intervention is

given to only one group, you can never really be

sure that something else did not coincidentally

occur at the same time to cause the measured

effect. Even when you are using a control group,

something could still happen to only the

intervention group (besides the intervention

itself) that affects the outcome. 

When the intervention’s introduction is

staggered, with the apparent effects

correspondingly staggered, history effects are an

unlikely explanation for the result. This is

because one coincidence of the intervention and

an extraneous event happening close together in

time is plausible, but two or more such

coincidences are much less likely.

Whenever a workplace or jurisdiction has more

than one division or group, a staggered

introduction of the intervention should be

considered as an alternative to introducing it to

all divisions or groups at the same time. This

staggered arrangement can also allow an interim

assessment and, if appropriate, modification of

the intervention or its implementation, before it

is introduced into other divisions (though such

modifications should be considered in the

analysis and interpretation of results). 

Chapter 4 Quasi-experimental and Experimental Designs

33
Quasi-experimental and Experimental Designs Chapter 4

34

15 Example from Komaki J, Barwick KD, Scott LR [1978] A behavioral approach to occupational safety: pinpointing and reinforcing safety

performance in a food manufacturing plant. Journal of Applied Psychology 63:434- 445. Copyright © 1978 by the American Psychological

Association. Adapted with permission.

Example of a multiple baseline across groups design15

A safety behavior training intervention was undertaken at a food manufacturing plant. The

intervention was first introduced in the wrapping department and then in the make-up department.

The intervention started with an educational session on safety behaviors, after which a list of safety

behaviors was posted. From then on the group was given feedback by posting the results of behavioral

observations. 

Safety behaviors were measured by a trained observer (three to four times a week). The observer

used a checklist which gave an estimate of the percentage of incidents performed safely. Baseline

measurements of safety behaviors were taken prior to introduction of the intervention. 

You can see how, in each department, the change in safety behaviors followed implementation of the

intervention. Having this sequence of events happen not only once, but twice, bolsters the causal link

between intervention and behavior change. Further, because implementation occurred at different

times, we really end up with two separate estimates of the amount of change caused by the

intervention. [The reversal part of the intervention will be discussed in Section 4.2.4]
4.2.4 Strategy #4: Reverse the intervention 

One way of strengthening a before-and-after or

even a time series design is to follow the

introduction of an intervention with another

phase of the project in which the intervention is

removed. In the simplest case, you end up with

three phases: a baseline phase; an intervention

phase; and a reversal or withdrawal phase. The

rationale here is that if you remove the

intervention conditions, you should

correspondingly see a change in the outcome

back towards the baseline condition. 

Of course, this design is clearly not suitable for all

situations, because it is hoped that the effect of

an intervention will last and therefore is not

easily reversed. However, as the Figure in section

4.2.3 shows, it has been found useful when

behavior is the safety outcome being measured.

In this case, the intervention was “reversed” by

no longer giving the posted feedback. 

Advantages and disadvantages of designs

with a reversal phase

If you can demonstrate the effect of a reversal

phase, you will have markedly reduced several of

the internal validity threats discussed in Chapter

4 - in particular history, maturation, testing,

dropout and Hawthorne (assuming

researchers/outsiders are still present during

reversal phase). Instrumentation and placebo

effects may still remain as issues and should be

considered. After demonstrating the effect of

intervention reversal, you are then free to

reinstate the intervention.

The downside to the reversal design feature is

that repeated changes in safety programming

could create confusion, stress and resentment

among those affected. As well, if an intervention

has looked promising following its introduction,

subsequent removal could be considered

unethical. Thus, use this design feature with

caution.

4.2.5 Strategy #5: Measure multiple outcomes 

The final strategy for increasing the strength of an

evaluation design is to use more than one type

of outcome measure. We describe two

approaches to doing this.

4.2.5.1 Add intervening outcome measures

We pointed out, using models in Chapter 2, that

there can be a number of outcomes intervening

between an intervention and the final outcome.

We should ideally try to measure as many of

these different intervention outcomes as is

feasible, in order to bolster the strength of

evidence provided by the evaluation design. This

includes measurement of the intervention’s

implementation, as well as short- and

intermediate-term effects of the intervention. 

Measures of intervention implementation, such

as the documentation of equipment purchases

and work task modification in the following

example, are especially important. In instances

where a program has failed, you want to be able

to distinguish between an inherently ineffective

program and a flawed implementation. If an

intervention has not been implemented as

intended, measuring effectiveness by measuring

changes in outcome will likely underestimate the

intervention’s potential impact. Thus, if

inadequate implementation is found by the

evaluation, you might try first to improve this

part of the intervention, instead of discarding the

intervention altogether. 

Chapter 4 Quasi-experimental and Experimental Designs

35
4.2.5.2 Add a related but untargeted outcome

measure

The second approach to adding outcome

measures involves measuring an outcome which

is similar to the main outcome measure, but not

targeted by the intervention. The additional

outcome measure should be similar enough to

the main outcome measure so that it is

susceptible to the most important threats to

internal validity. However, it also needs to be

different enough that it should be unaffected by

the intervention. The following examples show

how this approach works.

Quasi-experimental and Experimental Designs Chapter 4

36

A company plans to implement a

participatory ergonomics program. Plans

involve forming a labor-management

committee, assessing employee needs,

purchasing new equipment, modifying work

tasks and providing worker education. The

health and safety coordinator plans to

measure the ultimate impact of the program

by comparing self-reported symptoms and

injuries before and after the intervention is

implemented. 

However there are concerns that a change in

symptom and injury rates could have a

number of alternative explanations, such as

staffing changes, the business cycle,

management changeover and Hawthorne

effects, etc. To deal with this concern, the

health and safety coordinator plans some

additional measurements: records of

equipment purchases; and self- reports of

work tasks, practices and stressors. These all

measure outcomes intervening between the

intervention and the final outcome of changes

in symptoms and injuries.

Example of adding intervening outcome

measures

Mason [1982] tried to evaluate the

effectiveness of a train-the-trainer kinetic

handling training course, by looking at the

change in the rate of back and joint injuries in

the companies of instructors who had taken

course. When practically no change was

found after a year, it was valuable to know

that this was probably because few of the

instructors had organized and carried out incompany courses based on their own training

during that year. Furthermore, those who did

run courses had failed to retain most of their

training and therefore could not pass on the

handling techniques. The lack of any

measurable effect of the intervention on

injuries was therefore no proof that the kinetic

handling technique itself was not effective,

but rather that an improvement in the training

methods for trainers were needed.

Illustration of the value of measuring

intervention implementation
4.3 Experimental designs

Two key features of an experimental design are 1)

the use of a control group and 2) the assignment of

evaluation participants to either intervention or

control groups through randomization, a process

in which participants are assigned to groups in an

unbiased manner.18 Thus, an experimental

design uses an approach similar to strategy #1 in

quasi-experimental designs (Section 4.2.1). 

The use of randomization gives the experimental

design greater strength. We can be more certain

that any differences between the intervention

group and the control group, with respect to the

apparent effect of the intervention, can be

attributed to the intervention, and not to group

differences. Although it is often not feasible to

use an experimental design, it has been used in

several occupational safety situations. 

4.3.1 Experimental designs with “before” and

“after” measurements 

Earlier, three types of quasi-experimental designs

were discussed that use non- randomized control

groups: pre-post with non-randomized control

group (Section 4.2.1), multiple time series (4.2.2)

and multiple baseline across groups (4.2.3).

These same design approaches can turned into

experimental designs by using randomization to

create the groups. 

The first design shown in Figure 4.3, “pre-postwith-randomized-control” has been used in the

subsequent examples. The first example involves

randomizing work-sites into groups, and the

second, randomizing individuals into groups.

Chapter 4 Quasi-experimental and Experimental Designs

37

1)16 The effect of new equipment on oil-drilling platforms was primarily evaluated by changes in the

rate of tong-related injuries, a type of injury which should have been reduced by using the new

equipment. The rate of non-tong-related injuries, a related but untargeted outcome measure, was

also tracked. Although this second type of injury should have been unaffected by the intervention,

it would likely be similarly susceptible to any history or reporting effects threatening the internal

validity of the evaluation. Thus, including this untargeted injury measure in the evaluation

reduced these threats, since any history or reporting effects on tong-related injuries would also be

detected by changes in the non-tong-related injuries.

2)17 An ergonomic intervention among grocery check stand workers was primarily evaluated by

measuring self-reported changes in musculoskeletal discomfort. The intervention appeared

successful because of significant change in reported symptoms in the neck/upper back/shoulders

and lower back/buttocks/legs, the two areas predicted to benefit from the ergonomic changes.

This conclusion was bolstered by a finding of no significant changes in symptoms in the

arm/forearm/wrist, which were not targeted by the intervention. This made history, maturation,

instrumentation, placebo, Hawthorne and instrumentation effects a less likely explanation for

the improvement in the upper extremity and lower back areas. 

Examples of adding related but untargeted outcomes

16 Based on Mohr and Clemmer [1989] 17 Based on Orgel et al. [1992] 18 Randomization is discussed in Section 5.4.
Quasi-experimental and Experimental Designs Chapter 4

38

Figure 4.3: Experimental designs with “before” and “after” measurements

Example of an experimental design (1)19

An intervention for principle farm operators and their farms consisted of an on-site farm safety check

with feedback and a one-day educational seminar. Potential participants in the intervention were

identified from a list of all farms in the Farmers Association, using a random selection process. Of these,

60% of farm operators agreed to participate in the study. They were then assigned to either an

intervention or control group, using a randomization procedure. To evaluate the intervention, these

groups were compared on measures taken before and after the intervention: self-reported injuries and

near-injuries (final outcome) and safety perceptions, practices and attitudes (intermediate outcomes). 

19 Adaptation of intervention described in Glassock et al. [1997]

Table 4.3 Example of an evaluation of a farm safety intervention using an 

experimental design
Chapter 4 Quasi-experimental and Experimental Designs

39

Example of an experimental design (2) 20

Two interventions for the prevention of back injury were evaluated with an experimental design

involving warehouse workers for a grocery distribution center. Ninety workers with the same job

classification were randomly selected from among the 800 employees at a warehouse. The ninety

workers were then randomly assigned to one of three groups. One group was given one hour of

training on back injury prevention and body mechanics on the job. A second group was also given the

training, as well as back belts to wear. The third group served as a control group, receiving neither

training, nor back belts. Both “before” and “after” measurements were taken: knowledge (short-term

outcome); injuries and days absent as reported in health records (final outcomes). Abdominal strength

was also measured in case it decreased as a result of wearing the belt (unintended outcome).

20 Based on Walsh and Schwartz [1990]

Table 4.4 Example of an evaluation of back belt and training interventions using an

experimental design

4.3.2 Experimental designs with “after”-only

measurements 

One advantage of randomization is that in some

situations it may allow for not having “before”

measurements. This can be especially

advantageous if you are worried about the

measurement influencing the outcome of interest

(“testing effect”, section 3.5.4). It is also

advantageous if taking a before measurement is

costly (e.g., the administration of a

questionnaire).

The disadvantage of not obtaining “before”

measurements is that it will not be possible to see

if the groups differed initially with respect to the

outcome measure. You would therefore not be

able to make any allowance in the analysis for

these group differences. 
4.4 Threats to internal validity in

designs with control groups

We discussed how designs that use control

groups can markedly reduce the threats to

internal validity discussed in Chapter 3.

However, using control groups introduces some

new threats to internal validity which we

consider below. In spite of these, control groups

are still strongly recommended. On balance, they

strengthen the evaluation design far more than

they weaken it.

4.4.1 Selection threats

A selection threat occurs when the apparent effect

of the intervention could be due to differences in

the participants’ characteristics in the groups

being compared, rather than the intervention

itself. For this reason, control and intervention

groups should be similar, especially with respect

to any variables that can affect the measured

outcome(s).21

Whenever you compare groups created through

a non-random process, as in the quasiexperimental designs, you must consider how

selection could affect your results. In what way

do the people in the groups differ? Do they differ

in their initial value of safety outcome measure or

other characteristics (e.g., age, level of

experience, level of education, etc.) which could

influence the way groups respond to the

intervention? If so, you need to collect

information on these differences and make

allowances for these differences in your statistical

analysis.

Even by using a randomization procedure to

create groups, as in a true experiment, you can

have a selection threat.

4.4.2 Selection interaction threats

We just described how it is important for groups

to be similar in their characteristics at the outset

of an evaluation. It is also important that they

remain similar and are treated similarly over the

course of the evaluation. Otherwise, selection

interaction-effects threaten the legitimacy of your

evaluation conclusions. Recall that there are a

variety of threats to internal validity in beforeand-after designs, e.g., history, instrumentation,

dropout, etc. In many cases having a control

group - especially a randomized control group -

can reduce or eliminate these threats to internal

validity. The exception to this situation is when

something happens to one group (e.g., history,

instrumentation, maturation, etc.) and not to the

other, resulting in selection interaction threats;

i.e., selection-history, selection-instrumentation,

selection-maturation, etc.

For example, a selection-history effect could occur

if you are comparing two different divisions in a

“pre-post with non-randomized control group”

design. What if the supervisor of only one of

these divisions changed during the course of the

evaluation? You could not be sure whether

between-group differences in the “before” to

“after” changes was due to the effect of the

intervention on the intervention group - or due to

a change in the leader in one group. Selectionhistory interaction threats to internal validity are

often beyond the evaluator’s control, as in the

example above. If they should arise, they are

dealt with as was described for history threats

(Section 3.5.1).

A regression-to-the-mean-interaction threat to

internal validity arises if you deliver an

intervention to units with high injury rates and

compare their results to units with lower injury

rates. Even if there was no intervention effect,

the high injury group would tend to have a

decrease in rates, and the others might have even

shown an increase. The proper control group

Quasi-experimental and Experimental Designs Chapter 4

40

21 Depending on the type of evaluation design and the context, these characteristics or variables are sometimes called confounders; other times

they are called effect modifiers or moderating variables.
would be a second group with similarly high

injury rates.

Adropout interaction threat arises if one group has

a greater rate of dropout than the other, especially

if it results in the two groups having different

characteristics. Characteristics of particular

concern are those which could affect how the

study participants respond to the intervention

(e.g., age, level of experience, level of education),

as well as differences in the initial value of the

safety indicator used to measure outcome. While

these differences are sometimes taken into

account in the statistical analysis, it is preferable

to avoid selection-dropout threats to internal

validity altogether by taking steps to ensure that

people continue participating in the intervention

project and its evaluation.

Most other selection interactions, i.e., selectioninstrumentation, -testing, -placebo, - Hawthorne,

or -maturation effects can be minimized by

treating the control group as similarly as possible

to the intervention group with the exception of

the intervention itself. Ideally, the evaluators

should have just as much contact with

individuals in the control group as those in the

intervention group. In practice, such an

arrangement may not be feasible.

4.4.3 Diffusion or contamination threat 

A diffusion threat to internal validity (also known

as a contamination threat) occurs when the

intervention delivered to one group “diffuses” to

the other. This can easily happen when the

intervention is educational in nature, since

workers naturally share information with one

another. It is even possible for new equipment

given to the intervention group to be shared with

the control group. Diffusion is most likely to

occur when the intervention is perceived as

beneficial. It is undesirable for an evaluation

because it reduces the differences observed

between groups in their “before” to “after”

changes. Thus, you might conclude that an

intervention was ineffective when it really was

not. The best way to reduce the threat of

diffusion is by keeping the intervention and

control groups as separate as possible. 

4.4.4 Rivalry or resentment threat

Finally, threats to validity can arise when people

in the control group react to not receiving the

intervention. Suppose a safety incentive program

has been introduced to encourage safe behaviors.

The control group could react by not reporting

injuries so its safety performance ends up looking

good compared to the intervention group. Or the

opposite might be done. Injuries could be “overreported” to demonstrate that the group needs

an incentive program as well. In both cases we

could say that the control group has changed its

behavior due to rivalry. Resentment effects are

also possible. The control group, for example,

could resent not being given the opportunity to

participate in an incentive program. This souring

of labor-management relations in the division

could cause an increase in injury rates.

Rivalry or resentment threats can affect the

evaluation’s conclusions in either direction.

Depending on the situation, they can either

increase or decrease the differences between

groups in “before” to “after” changes. The effects

just described can sometimes be avoided by

communicating well with groups or promising

that if the intervention is shown to be effective,

the control group will receive the intervention

afterwards. If interventions are conceived and

introduced through a participatory process,

unexpected reactions are less likely. However, it

is impossible to anticipate every reaction to a

program. This is one area where qualitative

investigation can be very helpful. Interviews

with a few knowledgeable people in the control

group should give insight into whether rivalry

or resentment dynamics are an issue. As with

the diffusion threat, the rivalry or resentment

threats might be avoided if groups in different

locations are compared and communication

between the groups does not occur.

Chapter 4 Quasi-experimental and Experimental Designs

41
4.5 Summary

A quasi-experimental or experimental design is

more likely to give a truer estimate of the effect of

an intervention than a non-experimental design.

You can change a (non-experimental) before-andafter design into a quasi-experimental one

through one or more of the following design

strategies: adding a control group; taking more

measurements; staggering the introduction of the

intervention; reversing the intervention; or using

additional outcome measures. By adding these

design elements you can increase the strengthen

the design and reduce or eliminate the threats to

internal validity discussed in Chapter 3. 

Experimental designs differ from quasiexperimental designs by always involving a

control group and by assigning subjects to

intervention and control groups under a

randomization scheme. Otherwise, many of the

elements of quasi-experimental and experimental

designs are the same. Although some new

threats to internal validity need to be considered

when using designs with control groups -

selection, selection interactions, diffusion, rivalry,

resentment - the use of control groups is almost

always recommended whenever feasible. 

Quasi-experimental and Experimental Designs Chapter 4

42

• Improve upon a simple before-and-after design, and use a quasi-experimental design, through one

or more of five strategies: 

• adding a control group

• taking more measurements

• staggering introduction of the intervention among groups

• adding a reversal of the intervention

• using additional outcome measures.

• Improve upon a quasi-experimental design, and use an experimental design, by assigning

participants to intervention and control groups through randomization.

• Check that intervention and control groups receive similar treatment throughout the evaluation

period, apart from the intervention itself.

• Avoid (but check for) diffusion, rivalry or resentment effects.

Key points of Chapter 4
43

Study sample:

Who should be in your intervention

and evaluation?

Chapter5

5.1 Introduction

5.2 Some definitions

5.3 Choosing people, groups or workplaces for the study

sample

5.3.1 How to choose a (simple) random sample

5.3.2 How to choose a stratified random sample

5.4 Randomization - forming groups in experimental designs

5.4.1 Why randomize?

5.4.2 Randomized block design and matching

5.5 Forming groups in quasi-experimental designs

5.6 Summary
5.1 Introduction

Having decided on the evaluation design, you

should choose which individuals, work groups

or workplaces will be included in the evaluation

project. They comprise the study sample. This

chapter will discuss how to select the study

sample from a larger group of possible

participants, and how to form different

comparison groups within the study sample,

through randomization and other means. 

5.2 Some definitions

Let us start by distinguishing three terms:

1) The target population22 consists of the people,

groups or workplaces which might benefit

from the safety intervention. For example, if

you identify a safety need for construction

workers and conduct an intervention among

a participating group of workers, you want

it to apply to all construction workers. The

target population is “all construction

workers” in this case.

2) The sampling frame is a segment of the target

population - e.g., construction workers in a

given company, union, or city. 

3) A further subset, the study sample includes

those people, work groups or workplaces

chosen from the sampling frame. 

In summary, the study sample is a sub-group of

the sampling frame, which in turn is a sub-group

of the target population.

5.3 Choosing people, groups or

workplaces for the study sample 

The people or workplaces included in the

evaluation may be determined by circumstances.

For instance, if your concern is a single

workplace, and a decision has been made to

introduce the intervention to all its 50 employees,

then your study sample has been predetermined. However, in dealing with a large

workplace, it might not be necessary to include

everyone in the evaluation, if lower numbers (i.e.,

a smaller sample size) provide you sufficient

statistical power (see Chapter 8) to detect an

intervention effect. This is especially worth

considering if a measurement on larger numbers

of people increases the cost of data collection or

otherwise makes it unfeasible. Thus, situations

will arise where you need to select a study

sample for evaluation purposes from among all

participants in the intervention. 

The study sample should be representative of the

sampling frame and/or target population. This

is because more is required than just knowing

whether the intervention or program worked

only for the particular group selected for the

study and their particular circumstances (e.g.,

time, place, etc.). A bigger concern is whether

the intervention is generally effective. In other

words, you want the results to have

generalizability - also known as external validity.

Safety managers will want to know that the

evaluation results, obtained with a sample

selected from among their employees, applies to

their workplace as a whole. Someone with a

multiple workplace perspective - i.e., a

researcher, corporate safety director or policymaker - will want the results to apply to the

whole target population.

How can the sample be made representative of

the sampling frame? Suppose a training

intervention is being implemented for safe work

practices, and you will evaluate it by observing

workers doing their job before and after the

intervention. You have determined it is not

feasible to observe all of them going through the

program; so you limit yourself to a smaller

sample. 

You could ask for volunteers, but they will

Study Population Chapter 5

44

22 Note that the term target population is not always defined this way. Some people define it as what we are calling the sampling frame.
probably be unrepresentative of all the workers,

since they are more likely to have particularly

good work practices. Another alternative is to

choose everyone who works in one area (making

it easier to do the observations). But again, this

group is unlikely to represent the whole

workplace, given the wide variety of jobs. 

The best method is to choose a random sample,

which increases the chance of a representative

sample from the target population. This avoids

choosing subjects on any other basis (e.g.,

volunteering).

Using a control group, as well as an intervention

group, in your evaluation design, will increase

the required sample size.

5.3.1 How to choose a (simple) random

sample

Random selection involves choosing your sample

where each person in the sampling frame has a

known probability of being selected. With simple

random sampling, the most common type of

random sampling, the probability of being

selected is equal for everybody. The process is

similar in many ways to tossing a coin for each

person in the sampling frame and choosing those

people for whom the coin comes up heads. But

with coin-tossing the probability of getting heads

is 0.5 and of getting tails is also 0.5. We may only

want to choose 50 out of 200 people, so the

probability of selection in this case is one in four.

There are several different ways to choose a

random sample. One of the simplest is to use

random number tables, which typically show many

thousands of randomly selected digits. This

means that when the tables are generated, there

is exactly a one-in-ten chance (probability) that

each of the digits 0,1,...,9 would be selected for

any position on the table. The digits are usually

shown in groups of 5 - this has no particular

meaning - it simply makes the table easy to use.

Random number tables are often included in the

appendices of statistics text books. Alternatively,

many statistical or spreadsheet software packages

have a function which generates random

numbers. We used one to generate Table 5.1.

Chapter 5 Study Population

45

Considerations when choosing the study

sample

• To what target population will the results

be generalized?

• How many participating individuals,

workgroups or workplaces are potentially

available for the intervention and

evaluation?

• What sample size will give sufficient

statistical power?

• What is the marginal cost per participant

of data collection? 

• Will a control group be used in the

evaluation design?

• Will the sample be stratified?
5 8 5 0 1 4 2 5 4 9 8 1 2 0 0 7 9 0 5 6 1 1 0 7 0 7 6 0 8 1 

9 9 3 7 1 6 1 6 9 0 8 6 9 5 5 6 4 2 0 4 5 7 2 0 9 8 5 8 5 1

4 6 0 0 6 2 9 0 9 7 9 6 1 2 8 6 3 3 5 6 5 8 2 1 9 6 3 7 4 3

9 8 0 6 3 0 0 9 1 3 1 3 5 1 7 4 4 4 5 2 4 4 1 9 6 9 2 4 0 5 

1 9 0 0 0 6 5 3 9 1 7 8 9 6 2 1 7 4 0 0 1 7 3 7 3 5 2 6 9 0 

5 8 0 5 8 7 3 5 2 6 4 4 7 9 9 0 2 3 5 5 6 8 1 3 4 5 5 1 2 1

2 4 3 4 8 5 0 1 3 4 2 6 7 3 4 4 0 0 5 0 4 6 3 6 0 5 3 4 5 7

2 4 4 3 3 2 2 1 2 3 0 6 2 9 6 3 0 4 4 2 1 2 3 5 3 5 0 5 0 4

3 7 2 6 7 6 8 2 8 5 0 9 7 1 7 1 9 8 6 8 4 8 3 6 6 0 3 1 6 7

0 9 3 0 4 1 7 6 9 9 4 6 3 6 5 7 1 5 9 0 8 5 5 7 7 0 7 1 9 3

2 1 4 7 7 3 9 8 0 5 4 9 8 1 2 5 2 9 0 0 5 4 7 6 9 5 3 4 1 1 

8 6 2 4 4 6 6 9 5 1 4 6 3 3 1 7 6 1 2 4 2 6 8 2 5 4 5 5 1 8 

0 7 5 1 0 0 1 8 3 9 9 5 7 2 5 2 2 1 3 4 4 5 7 5 2 8 8 2 0 3

9 5 8 4 0 5 3 0 1 7 8 2 1 3 1 7 4 4 8 7 4 2 2 8 3 6 8 6 3 7

0 5 4 8 4 6 4 9 6 8 4 0 2 9 8 7 1 9 1 8 3 4 5 5 3 3 2 4 8 5

8 6 0 7 0 8 3 1 2 7 0 1 1 2 3 0 2 1 3 3 0 8 4 6 9 6 8 2 9 0

8 7 5 7 5 3 0 3 7 4 3 3 7 3 0 0 9 4 4 1 9 2 5 1 9 4 1 6 6 5

6 8 5 4 4 7 6 7 4 6 3 4 0 6 3 5 5 2 1 9 4 5 7 6 5 4 7 2 3 0

3 3 6 7 9 7 8 4 7 6 4 7 8 6 7 1 9 4 4 8 9 4 2 1 8 2 9 5 3 6

8 5 1 4 3 9 6 1 2 2 0 5 7 4 5 7 7 2 6 0 7 4 0 9 2 4 8 7 5 3

3 1 8 9 4 6 7 5 2 2 8 2 2 8 6 7 7 4 1 4 1 5 3 7 2 3 5 7 7 9

7 8 6 8 3 4 9 3 2 9 4 5 4 8 2 5 7 8 2 6 5 5 1 4 2 8 6 0 7 6 

7 0 1 3 5 6 1 5 6 3 7 1 8 8 5 3 8 8 1 5 5 1 2 7 5 7 1 4 1 0 

7 7 3 1 0 9 9 0 9 6 9 4 5 5 6 2 7 8 7 5 0 6 9 3 9 6 7 1 2 5

3 6 9 6 8 5 1 9 9 1 9 7 2 7 4 2 9 2 7 0 8 0 4 8 6 2 4 4 5 6

3 8 2 8 7 8 0 7 5 4 5 1 4 2 2 4 1 3 9 0 4 9 8 4 3 5 1 9 3 9

9 6 3 6 7 3 1 2 7 7 5 5 9 5 8 5 1 1 7 5 4 7 0 9 6 1 3 5 7 4

6 0 4 8 8 3 5 6 1 9 9 5 3 7 4 2 6 4 4 4 0 3 7 9 3 6 4 2 8 4

5 7 9 7 5 8 3 6 9 8 8 0 5 2 1 7 0 3 5 3 2 6 2 5 1 5 7 2 6 2 

0 7 3 6 4 3 7 1 9 4 9 9 1 5 6 3 5 1 7 0 9 0 9 4 1 2 9 5 5 8 

Study Population Chapter 5

46

This table was generated using a spreadsheet software with a random number generation function. It can

be used for selecting a random sample from a sampling frame and for randomizing sample subjects to

intervention and control groups. The groups of three digits indicated above are used in the illustration

of random sampling in Section 5.3.1.

Table 5.1 Random number table
5.3.2 How to choose a stratified random

sample

Random sampling is not guaranteed to produce

a sample representative of the sampling frame,

although it does work “on average.” That is, if

we repeat the procedure many times, the average

proportion of women in the samples is the same

as their proportion in the sampling frame as a

whole. When a fairly large sample is chosen,

representativeness is more likely. However, with

small samples, this may not be the case. To avoid

the problem of lack of representativeness, select

a stratified random sample. This allows you to

deliberately select a sample with the same

proportion of men and women as in the total

group. 

Do this by stratifying the group into the two sexes.

Then choose a sample of men, and a sample of

women, applying the same process as in simple

random sampling with each stratum. The first

sample has the number of men you want; the

second, the number of women. Opinion polls

typically use some form of stratified sampling,

though one that is rather more complex than has

been described. 

(Caution: with stratified sampling, the statistical

approach you use to analyze the data must be

modified.)

Another reason for stratifying would be if there

are important differences in the reaction of subgroups to an intervention, and one of the subgroups in the sampling frame is quite small. For

instance, suppose you want to look at the effect

of flexible work hours on both men and women

in a manufacturing environment by means of a

survey, yet women comprise only 5% of the

working population. You would end up with

about 10 women, if 200 workers were selected at

random from the total work force, making your

estimate of the effect of the intervention on

females in your sample imprecise. 

However, the precision could be greatly

improved if you first stratify by sex and then

choose 50 women and 150 men, using random

sampling from each stratum. 

Chapter 5 Study Population

47

How do you randomly select, say 50 people (the study sample) from a group of 839 workers (the

sampling frame)? To do this, you can use a random number table, such as the small one provided here

(Table 5.1). Typically, you start using the table at an arbitrary point, determined by, for example, rolling

a die. You can roll to see which of the large groups of rows to select, and then roll three more times to

similarly select the exact row, the group of columns and the exact column. If you rolled 3, 4, 5, 4, you

would start at the third group of rows, 4th row, 5th group of columns and 4th column ending up at the

number 8.

Since the sampling frame contains 839 workers, number them from 1 (or rather 001) to 839. The number

839 is less than 1000, so you can go through the table, using three digits at a time. Reading from the

table then, you would read off the following sequence of numbers to start: 836, 863, 705, 484, 649, 684,

029, 871, 918, 345, 533, 248, 586. Ignore digit triplets lying between 840 and 999, as well as 000. This

means you would select for your sample, the workers numbers 836, 705, 484, 649, 684, 029, 345, 533,

248, 586. You could continue until you have the 50 people required. If the random number table should

yield a repeated triplet of digits, ignore this and use the next valid triplet.

How to select a random sample using a random number table
5.4 Randomization - forming groups

in experimental designs

You have seen how to randomly select a single

sample from a bigger group. Suppose, you do

an experiment, with one intervention group and

one control group. In this case, you randomize

study subjects (i.e., workers, work groups, or

workplaces) to either group and make sure they

all have the same chance (probability) of being

assigned to each one. Typically, these

probabilities will be one half, or equal for each

group. It is rather like tossing a “fair” coin -

heads you go in the intervention group, tails you

become a control.

5.4.1 Why randomize?

Why randomize subjects into intervention and

control groups? The primary purpose is to avoid

selecting only particular types of people. For

example, we do not want only volunteers for the

intervention group, leaving other people for the

control group. Volunteers differ in many ways

from non-volunteers. Similarly, we do not want

all the men in one group and women in the other.

We even want to avoid the tendency for men to

be in one group rather than another.

You might argue that you can certainly tell if

subjects are men or women, and thus check for

any imbalance of the two sexes in the treatment

and control groups. But what about factors you

do not measure, or do not even know about or

cannot measure? The answer is that with

randomization it does not matter! This is because

on average these factors balance out if you

randomize. When we say on average, we mean: if

we repeat the randomization many times, and

each time calculate the resulting proportion of

men in the treatment and control groups, the

average of all these proportions for the

intervention group would be the same as that for

the control group. Similarly, the average

proportion of women in the intervention and

control groups would be equal, following many

randomizations. This is true of variables we have

not measured.

Study Population Chapter 5

48

Suppose you want to randomize people into two groups, with an equal probability of selection into

either. As with random selection, there are several ways we can proceed. Using the random number

table (Table 5.1), you could start at the point where you left off in choosing your random sample and

read off the sequence: 070 83127 01123 02133 08... Taking single digits, if the digit is even (including 0)

you allocate the person to the intervention group. If the digit is odd you allocate to the control group.

Alternatively, our rule could be that if the digit is between 0 and 4, the subject goes in the intervention

group; if between 5 and 9, the subject becomes part of the control group.

We will illustrate this using the odd/even rule and allocate 20 people into two groups, 10 per group.

First, number the 20 people 01 to 20. The first digit in the random number sequence is 0, so subject 01

is assigned to the control group; the second digit is 7 so subject 02 is in the intervention group.

Continuing, you see that subjects 02, 05, 06, 08, 10, 11, 13, 14, 16, 17 are put into the intervention group.

Since you now have ten people in this group, you can stop the randomization and put the three

remaining subjects in the control group. Sometimes, you will decide in advance to randomly allocate

people to groups without guaranteeing equal numbers in each group. If you did this here, you would

keep selecting single digits so that subject 18 would also go into the intervention group and subjects

19 and 20 would go in the control group. This means that out of 20 people, eleven are in the intervention

group and nine are in the control group. There is always the risk of an imbalance like this, particularly

with small samples.

How to randomize
Sometimes, you might see a study where, even

though proper randomization techniques have

not been used, it seems that there is no biased

pattern of selection into the treatment or control

group. Why is this still not as good a design?

The problem is that there may in fact still be some

selection bias. For example, someone may have

deliberately (or even sub-consciously) put into

the intervention group people considered more

interested in safety. This will mean the groups

are not truly comparable.

5.4.2 Randomized block design and matching

You may want to ensure that a characteristic, such

as sex, is balanced between the groups, in order

to avoid a selection threat to internal validity.

Thus, in this case you want equal numbers of

men in both intervention and control groups;

and, similarly, equal numbers of women in each

group. How can you guarantee this?

The answer is to stratify subjects and randomize

within the strata (or “block” in the jargon of

experimental design). What you do is list all the

men to be randomized and assign them in equal

numbers to intervention and control groups.

Then do the same for women, and you will have

a similar distribution of the sexes in each of the

groups.

Another possibility is to match. First, pair up

(match) subjects according to characteristics like

sex, age, duration of employment and so on. You

can then (randomly) allocate one member of the

pair to the intervention group, and the other to

the control group. (This process is really like the

randomizing within blocks, with each block

reduced to just two people). In practice, it can be

difficult to get exact matches. So instead of taking

people with the same year of birth, you may have

to match pairs to within two or three years in age. 

5.5 Forming groups in quasi-experimental

designs

It might be difficult or even impossible to match

or randomize subjects to one group or another,

given the requirements of a particular

organization of people at a workplace. Or a

group (e.g., department, work-site, etc.) might

have already been chosen to participate in the

intervention, thereby preventing any

randomizing of participants to intervention and

control groups. In such cases, you can still choose

another group, which will serve as the control

group, as in a number of the quasi-experimental

designs discussed in Chapter 4.

The overriding principle in choosing nonrandomized groups for a quasi-experimental

design is to make them truly comparable. They

should be similar in all respects apart from the

intervention. In comparing two departments, you

want them to be similar in their work activities.

You would not compare an accounts department

with a maintenance department. Of course

within workplaces there may be no directly

comparable groups - so aim to select ones that

closely resemble each other. You might even try

similar departments in other workplaces,

preferably from the same type of industry. 

The actual choice you make depends on your

local situation. We cannot say specifically what

group would be best, but several characteristics

can be considered.

Chapter 5 Study Population

49

• worker characteristics (e.g., age, sex,

experience)

• nature of job tasks

• work environment (i.e., exposure to

hazards, safety controls)

• workplace organization (e.g., structures for

decision-making and safety, work flow)

• contextual factors (e.g., health & safety

culture; management support for safety)

• past safety record

Characteristics to consider when choosing

a non-randomized control group
5.6 Summary

We have described how to randomly select

participants from a sampling frame. This is done

so that the study sample is representative of the

sampling frame and the intervention results will

be applicable to the larger group. We also

described how the process of randomization can

be used to create intervention and control groups

in experimental designs. For situations in which

groups are formed non-randomly, some

considerations were given. 

Study Population Chapter 5

50

• Choose your sampling frame, so that it is

typical of the target population to which

you want to generalize your evaluation

results.

• Select a study sample from your sampling

frame using random sampling.

• Whenever possible, use an experimental

design with randomization to assign

participants to intervention and control

groups.

• In quasi-experimental designs, select

intervention and control groups so that

they are similar.

Key points of Chapter 5
51

Measuring outcomes

Chapter6

6.1 Introduction

6.2 Reliability and validity of measurements

6.3 Different types of safety outcome measures

6.3.1 Administrative data collection - injury statistics

6.3.2 Administrative data collection - other statistics

6.3.3 Behavioral and work-site observations

6.3.4 Employee surveys

6.3.5 Analytical equipment measures

6.3.6 Workplace audits

6.4 Choosing how to measure the outcomes

6.4.1 Evaluation design and outcome measures

6.4.2 Measuring unintended outcomes

6.4.3 Characteristics of measurement method

6.4.4 Statistical power and measurement method

6.4.5 Practical considerations 

6.4.6 Ethical aspects

6.5 Summary
6.1 Introduction

Chapters 3 and 4 described the various study

designs used in evaluation. In those chapters,

we referred to taking measurements. This

chapter will discuss those measurements. We

will first introduce the concepts of reliability and

validity - two key characteristics to consider

when choosing a measurement technique. We

will then review several common ways of

measuring safety outcomes, examining reliability

and validity. Finally, we will list a wider range of

considerations in choosing your measurement

method(s).

Here, we will be discussing only quantitative

methods; i.e., those which yield numerical

information. The next chapter deals with

methods which yield qualitative information. A

comprehensive evaluation should include both

types of data.

6.2 Reliability and validity of

measurements

A measured value consists of two parts: the true

value plus a certain amount of measurement error

(i.e., the error we make in measuring). It is this

measurement error which makes a particular

measured value either higher or lower than the

true value. Thus, measurements are more

accurate when measurement error is minimized.

Imagine using a ruler to measure the legs of a

table. Since we do not measure them perfectly,

each estimate of leg length will consist of the true

value plus or minus a small amount of error.

Measurement error, in fact, consists of two parts.

One part is called systematic error, also known as

bias. This type of error exists when we

consistently make an error in the same direction.

This would happen, for example, if we always

looked at the ruler from an angle, causing us to

consistently underestimate the table leg length.

The other part of measurement error is random

error. As the name implies, it fluctuates

randomly, sometimes leading to overestimation,

and sometimes to underestimation. These two

types of measurement error affect the reliability

and validity of a measurement method. While

evaluating the effectiveness of your intervention,

apply measurement methods which minimize

both types of measurement error. In other words,

these methods should be valid and reliable.

Measurements that are valid have a low degree

of systematic error and measurements that are

reliable have a low degree of random error. In

other words, a valid method means we are

measuring what we had hoped to measure. A

reliable method gives us consistent answers

(while measuring the same thing) on numerous

occasions. If a measurement method is both valid

and reliable, it is considered to be accurate.

Figure 6.2 illustrates these concepts of reliability

and validity with the analogy of a shooting

target. Consider the center of the target as the

true value and the bullet holes as the actual

measured values. Reliable measurement has a

low degree of scatter to the values (as in the lefthand panels in Figure 6.2). Valid measurement is

centered on the true value (as in the top panels).

Quantitative Measurement Chapter 6

52

Figure 6.1:Types of error in

measurement
Why reliability and validity are important

Poor reliability is a problem for evaluation

because it makes it harder to detect any effect of

a safety intervention, even if it is truly effective.

This is because it is hard to tell whether any

changes in critical safety outcome measures are

due to the intervention or simply to random

fluctuation. Unfortunately, lost-time injury rate

data, except in larger workplaces, often has low

reliability. For this reason, alternative or

additional outcome measures must often be used

to measure the effect of an injury reduction

intervention.

When methods are reliable, but have poor

validity, your conclusions drawn from evaluation

results might be wrong, especially if you are

measuring a concept different from the one you

thought you were measuring.

Specific types of reliability and validity

There are several specific types of reliability

which may be of concern to evaluators: analytical

equipment reliability or precision, inter-rater

reliability, test-retest reliability and internal

consistency of questionnaires. We will elaborate

on these in our discussion about particular types

of outcomes measures.

Similarly, several types of validity can be at issue.

Major types are criterion, content and construct. 

• Criterion validity is the extent to which the

measurement predicts or agrees with some

criterion of the “true” value or “gold

standard” of the measure. For example, you

would establish the criterion validity of worksite observation measurements by showing a

correlation of these measurements with injury

rates in a given workplace.

Chapter 6 Quantitative Measurement

53

Figure 6.2: Illustration of the effects of reliability and validity on measurement
• Content validity is applicable only to

instruments like questionnaires or checklists.

It is concerned with whether or not they

measure all aspects of the concept(s) of interest.

This type of validity can be established by

having experts review the instrument for its

completeness of content.

• Construct validity is the hardest to establish, but

the most important. It pertains to how well the

measure accurately indicates the concept (or

construct) of interest. This is not an issue when

you are dealing with a concrete concept like

injuries. You already know that lost-time

injury rates are accepted indicators - assuming

the data are free from biases. On the other

hand, construct validity becomes more of an

issue whenever you are measuring abstract

concepts. For example, if the objective of the

intervention is to change the safety climate of

the workplace, you might want to measure the

outcome (safety climate) with a safety climate

questionnaire. This is a good idea, but you

need to determine how the construct validity of

the questionnaire was established. In other

words, how was it established that the

questionnaire truly measures “safety climate”

and not something more limited like safety

policy and procedures. 

6.3 Different types of safety outcome

measures

In the following, we discuss some of the more

common outcome measurement methods, with

a focus on the reliability and validity.

6.3.1 Administrative data collection - injury

statistics

Several types of injury statistics have become

standard reporting measures for companies.

They are often determined by legislative

requirements. The most common measure, injury

frequency rate, is equal to the number of injuries

per unit of exposure. There are different

categories of injuries where rates can be

calculated: e.g., lost-time or disabling injuries;

recordable injuries (i.e., those required by law to be

recorded); medical treatment injuries; and first-aid

only injuries. Although a less commonly accepted

standardized measure, near-injury rates can also

be calculated. 

Various units of exposure are used to calculate

frequency rates. Worker-hour units of exposure

- typically 100,000 worker-hours or 1,000,000

worker-hours - yield relatively precise frequency

rate estimates. However, the number of workers,

a cruder measure of exposure, is also used. The

choice between the two depends on the state of

record-keeping, with the former requiring good

records of worker-hours, including lay-offs,

overtime and lost time. The number of injuries can

also be used to compare two time periods of

equal length, but the equivalence of the workerhours of exposure during the time periods must

be confirmed.

Severity rate is another widely used injury

statistic. It is calculated by taking a ratio of losttime hours over the corresponding units of

exposure - the higher ratios corresponding to

greater severity. Severity rate is a useful

complement to frequency rate, since some

interventions can have an impact on severity, but

not on frequency. This could result, in some

cases, from the interventions affecting severity

more than frequency. It could also result from it

being easier to (statistically) detect an effect on

severity than frequency, for a given effect size.

Quantitative Measurement Chapter 6

54

1. Administrative data collection - injury

statistics

2. Administrative data collection - other

statistics

3. Behavioral and work-site observations

4. Employee surveys

5. Analytical equipment measurement

6. Workplace audits

Common safety outcome measurement

methods
Claims data collected by workers’ compensation

systems are useful for evaluating interventions

delivered to a multiple workplaces in a

jurisdictional area.

Validity and reliability concerns with injury

statistics

The major concern in using injury and claims

data involves the reporting biases that may exist

and stem from systematic errors which cause

injury records to be consistently different from

the true injury occurrence. Such biases can enter

at any point during the transfer of information -

from the time a worker experiences an incident to

when that incident becomes part of national

statistics. On the one hand, certain compensation

or work environments may encourage overreporting of injuries by workers. On the other

hand, incentives to individuals or organizations

to minimize injuries may encourage

underreporting of injuries or a reclassification to

a lower level of severity. In particular, incentives

for early return-to-work might result in the

recording of a medical-aid only incident, which in

the past or in a different location would have

been considered a lost-time injury.

The degree of underreporting can be a great

source of bias. One study of hospital workers’

data from self-report questionnaires showed that

39% of those who had experienced one or more

injuries did not report them.23 Although the main

reason for not reporting was that they considered

the injuries too minor, in fact, 64% of them

involved medical treatment and 44% lost work

time. In another study in the U.S.,24 OSHA 200

forms (U.S. workplaces are required to record

injuries and illnesses meeting certain severity

criteria for the Occupational Safety & Health

Administration) from several companies were

compared with company clinic records. This

showed that the OSHA logs had captured only

60% of the reportable injuries.

A filter model of the injury reporting process25

has been developed that can help identify the

places at which biases can influence injury

reporting and the reasons for these biases (Table

6.1). A filter in this model is anything which

prevents some of the reportable injury data at one

reporting level from passing to the next level of

reporting. For example, level one is considered to

represent the true injury rate, with the first filter

being the worker’s decision-making process

about whether to report the injury or not. The

second, third and fourth filters operate at the

workplace; the fifth at the transmission of

company-level data into aggregate data at the

jurisdictional level. The filters operate differently

for injuries of differing severity. The less severe

the injury the more effective and less consistent

are the filters. Accordingly, near-injuries are

especially prone to biased and inconsistent

reporting.

Often the presence of some reporting biases can

be tolerated in an evaluation - if they

continuously affect the data in the same way. A

problem arises if they operate differently, either

over time or between groups, for any of the

measurements being compared. Just how

differently they operate has to be estimated and

taken into account when interpreting results.

One special evaluation challenge in using injury

statistics are those cases where the intervention

itself has an impact on the way the filters operate.

Management audits, for example, tend to

improve reporting, while safety incentive

programs that reward workers or managers for

low injury rates discourage reporting. In such

situations it is important to include methods for

verifying the injury data, as well as to incorporate

supplementary outcome measurement methods,

not subject to the same type of biases. 

Chapter 6 Quantitative Measurement

55

23 Weddle MG [1996]. Reporting occupational injuries: the first step. J Safety Res 27(4):217-223. 24 McCurdy SA, Schenker MB, Samuels SJ [1991]. Reporting of occupational injury and illness in the semiconductor manufacturing industry. Am

Public Health 81(1):85-89.

25 Webb et al. [1989]
Quantitative Measurement Chapter 6

56

Table 6.1: The filter model for work injury reporting: six levels and five filters26

26 Reprinted from Accident Analysis & Prevention 21, Webb et al. Filtering effects in reporting work injuries, 115-23, Copyright 1989, with permission from Elsevier Science.
Misclassification errors can cause a problem in

injury statistics. Misclassification can be

attributed to errors or disagreement in the

judgement of people involved in abstracting

information from incident or clinical records, and

depends in part on the individual coders, as well

as on the classification scheme used. A common

method of classifying injuries and illnesses, the

International Classification of Diseases, 9th

revision (ICD-9) has been shown to perform

poorly for soft-tissue disorders, since several

different ICD-9 codes can be assigned for the

same condition.27 As well, the ability to code

incident descriptions consistently has been

shown to depend on which aspect of the incident

is being coded. Table 6.2 shows the percent

agreement in coding for two trained people

coding the same 100 injury reports using a

standardized coding scheme28. 

Coding is considered unreliable when scores are

less than 0.7. As you can see from Table 6.2, many

of the important items being coded fell below this

cut-off point. To improve the inter-rater

reliability, the coders may need more training or

the coding scheme may need revising. In

addition, you may want to maintain the same

coders through the data collection phase of the

evaluation, because a change in personnel could

have a large impact on the results. You should

also check for any changes in classification

practices over time or differences in the coding

practices between intervention and control

groups.

Checking the validity of injury statistics

before and during data collection

If you use injury statistics as an outcome measure

to evaluate the intervention, consider the

potential biases at the outset. Investigations of

data validity can be made beforehand, and, if

necessary, corrective steps taken to improve data

collection. However, if that is done, wait until

their impact on the resulting statistics has

stabilized. 

Also, check the validity of the injury statistics by

comparing them with data obtained at a lower

level of reporting - e.g., a comparison of the

frequency of incidents in summary statistics with

the medical or safety records on which the

statistics are based. Sometimes, several sources

are used to identify the complete universe of

incidents, after which you can determine how

well any single source captures them. You might

use supervisor, clinic and claims reports to

identify the universe of incidents in a workplace

and then see what percentage is captured by each

type of report.

Checking the validity of injury statistics after

data collection

Even after ensuring that the collected statistics

are consistent with respect to any biases, reality

might differ from expectation. Thus, it is a good

idea to check the data after it has been collected

as well. A good indicator of underreporting is

Chapter 6 Quantitative Measurement

57

Table 6.2: Reliability of coding injury

descriptions

Item being coded Reliability 

Sex 0.98

Year of birth 0.89

Industry classification 0.64

Injury location 0.64

Type of injury 0.92

Part of body injured 0.92

Injury legally notifiable or not 0.84

Agent of injury 0.79

Event precipitating injury 0.44

Contributory factors 0.61

27 Buchbinder R, Goel V, Bombardier C, Hogg-Johnson S [1996]. Classification systems of soft tissue disorders of the neck and upper limb: do

they satisfy methodological guidelines? J Clin Epidemiol 49:141-149.

28 Adapted from Glendon AI and Hale AR [1984]. A study of 1700 accidents on the youth opportunities programme. Sheffield: Manpower Services

Commission.
the ratio of minor to major injuries. Since minor

injuries are more likely to be “filtered out” than

major ones, a constant ratio indicates the stability

of any underreporting biases (or lack of them).

This method does depend on major injuries’

occurring frequently enough in the period

measured that they perform as reliable measures. 

Small numbers issue and injury statistics

Lost-time injuries and other severe injuries might

not be useful in effectiveness evaluations in

smaller workplaces. The small number of

injuries found in a smaller workplace leads to

statistical tests with low power. This means it will

be more difficult to detect an intervention effect,

even if the intervention is truly effective.

For this reason, people sometimes use the

frequency of less severe injuries, e.g., first-aidonly injuries, to evaluate safety intervention

effectiveness. However, less severe injuries are

more susceptible to underreporting biases than

more severe injuries. Thus, the opposing

considerations of statistical power versus validity

must be weighed when choosing measurement

methods. Examine both severe and minor

injuries if the data are available.

Another alternative or supplementary approach

to the small numbers issue, is to measure

intermediate outcomes, e.g., work practice

observations, work-site observations or safety

climate. Power will likely be greater in the

statistical tests on these data than on injury data.

Another advantage of this approach lies with the

location of the intermediate outcomes, which are

situated closer to the intervention than injuries

in the causal chain. The intervention effect is

therefore less “diluted” or attenuated by other

factors. The challenge in using upstream proxy

measures for injury outcomes is that a good

correlation has to be established between this

proxy measure and a more established measure

of safety such as injuries, in order to demonstrate

the validity of the proxy measure. We will

discuss some other measures below.

6.3.2 Administrative data collection - other

statistics

As discussed, there are some problems with

relying upon injury statistics for evaluating

workplace interventions. For this reason you

might choose other types of data found in

administrative records. In doing so you can

adopt the strategy, referred to earlier, of using an

intermediate outcome as a proxy for the final

outcome in the evaluation. Even when the injury

statistics serve as a final outcome measures,

additional administrative data can provide

insight on the way the intervention brought

about change. Finally, these data are often useful

for demonstrating that the intervention is being

implemented as planned.

As described in the above section, consider

whether any biases are entering the process of

collecting these data; and conduct validity checks

if needed.

Quantitative Measurement Chapter 6

58

29 Example from Menckel and Carter [1985]

Example of the use of other administrative

data29

Consider an example in which an incident

investigation intervention is being evaluated. A

new consultative group has been formed to assist

supervisors investigating incidents, with an aim to

improving the quality of actions resulting from

the investigation. The following quantitative

measures derived from administrative records are

included in the intervention evaluation: 1) time

between incident occurrence and formal reporting

of it; 2) the number of near-incidents reported; 3)

percentage of incidents for which corrective

measures were suggested. 

Change is seen in all these intermediate outcomes

in the direction that suggests that the intervention

has been effective. It is also found that the number

and severity of incidents (final outcomes) showed

a decrease, although only the latter is statistically

significant. Thus, even though the injury

frequency did not show statistical significance,

changes in the intermediate outcome measures (as

well as some qualitative evidence not discussed

here) together suggested that the intervention had

been effective.
6.3.3 Behavioral and work-site observations

Observations of worker safety-related behavior

are increasingly being used to measure the effect

of safety interventions, especially behavior-based

interventions. To use this method, you first

develop a checklist of behaviors that the

intervention is trying to influence. Targeted

behaviors are identified from incident

investigation reports, as well as from the opinions

of supervisors and workers. Be prepared to first

develop a trial checklist and make adjustments

according to feedback. This will ensure that the

list is comprehensive (improving its validity) and

the items are unambiguous (improving its

reliability). 

The checklist is then used by an observer (trained

supervisor, evaluator or worker) who visits the

work area at a randomly selected time of day and

makes observations for approximately half an

hour. For each behavioral item on the list, the

observer marks either “performed safely”,

“performed unsafely” or “not observed”.

Following the observation period, the proportion

of safe behaviors is calculated. It consists of the

ratio of the number of items performed safely

over the number of items observed.30

Another checklist approach uses observations on

the work-site conditions (e.g., housekeeping,

emergency equipment). Details of such a method

for the manufacturing industry can be found at a

site of the Finnish Institute of Occupational

Health:

www.occuphealth.fi/e/dept/t/wp2000/Elmeri1E.html.

Advantages and disadvantages of behavioral

and work-site observational measures

Observational measures offer several advantages.

First, they are “leading indicators” instead of a

“trailing indicators”, meaning you do not have

to wait until incidents happen to get a measure of

safety. Rather, measurement is “upstream” of

incidents in the causal pathway. Second, you can

take observations frequently, as often as several

times a week. This yields data sensitive to

changes caused by interventions and can be

analyzed for time trends. Third, there is some

evidence that behavior serves as a valid proxy

for injuries as a final outcome measure. Reviews

of injury records show that the majority of

injuries are associated with unsafe acts. [This is

not to say that responsibility for such injuries lies

exclusively with the worker carrying out these

unsafe acts. Conditions leading to these unsafe

acts are typically the responsibility of

management.] 

Further, evaluations of behavioral interventions

- at least the ones that have been published - tend

to find that an improvement in behaviors is

correlated with a decrease in injury rate.

Validation of work-site checklists using injury

rates as a criterion has also been achieved

[Laitinen et al. 1999a,b].

A drawback with behavioral observations is that

they are sometimes regarded unfavorably by

those being observed, and in some environments

could be considered unethical or otherwise

unacceptable. This is less of a problem with

work-site observations, because there is less

emphasis on the behavior of individuals. As

well, observations of the work-site can be carried

out in a less intrusive manner, thereby interfering

less in the measurement of the intervention’s

effect.

Chapter 6 Quantitative Measurement

59

30 See Krause [1995] for more details on this methodology.
Additional validity and reliability issues when

using behavioral and work-site checklists

There are additional methodological issues to

consider when using observational checklist

techniques. One is the inter-rater reliability of the

list. This is determined by having more than one

person observe the same area simultaneously and

independently record their observations. The

amount of agreement between the two raters can

then be compared. Typical ways of reporting

inter-rater reliability are the percent agreement

on items (the percentage of list items categorized

the same) or, better, by using a special statistic

known as a Kappa coefficient.

31 This statistic takes

into account the percent agreement that would

occur simply by chance before the percent

agreement is calculated. Kappa values between

0.40-0.59 indicate agreement which is moderate,

0.60-0.79 substantial and 0.80-1.00 very good. A

high reliability ensures that there will be little

variation in the data as a result of having different

observers carry out the observations. If this

reliability is low during the piloting of the

checklist, you should be able to improve it by

removing any confusing language or better

specifying criteria. 

In order for the checklist to be able to measure

change, avoid what are called ceiling effects. This

refers to the situation where you are unable to

detect an improvement of the index score,

because the initial measured values were already

high and have limited room for improvement.

Thus, you ideally want your pre-intervention

index scores to be around 50%. If they are higher

than 80% during the testing phase, see if you can

modify or substitute items so that they will be

more difficult to achieve and still be true to the

intervention’s aims.

Before accepting observations as the definitive

final outcome measure in evaluating an

intervention, you would want to determine if a

statistically significant correlation exists between

the behavioral index scores and injury rates. If

this is not possible beforehand, then collect some

kind of injury data during the evaluation, along

with the observations, in order to calculate such

a correlation. To get data yielding sufficient

statistical power during analysis, you might

require a measure of minor injuries, provided

that any underreporting biases remained

constant throughout the study.

6.3.4 Employee surveys

Employee surveys often measure what cannot

otherwise be observed. They examine the

knowledge, attitudes, beliefs, or perceptions held

by individuals. Occasionally, they assess group

phenomenons such as climate or culture. They

can also be used to measure (self-reported) safety

practices and injuries, both of which can also be

quantified by the methods discussed above. 

Surveys of knowledge are an appropriate final

outcome measure if the intervention is only

designed to change knowledge. A similar

statement could be made about surveys of

attitudes, beliefs, perceptions, practices, culture

or climate. However, if the intervention is

designed to ultimately affect worker safety and

injury rates, then one must be cautious about

using surveys which measure only knowledge,

attitudes, beliefs or perceptions as a proxy for

injury rates as a final outcome measure. Such

questionnaires have not usually been sufficiently

validated through correlation with injury rates

to justify their use in this way. 

Tips for better questionnaire data

In choosing from a number of possible

questionnaires, Exhibit 6.1 has some questions

that will assist you in that selection. They are

based on the assessment of the validity and

reliability of the proposed questionnaire. The

more questions to which you can answer “yes”,

the more likely the questionnaire is suitable for

Quantitative Measurement Chapter 6

60

31 Percent agreement and Kappa statistics are used with categorical data; correlation coefficients are used to measure the inter-rater reliability

of continuous data.
the effectiveness evaluation.

If you want to develop a questionnaire, consult

some specialized books on the subject, such as

the one by Aday [1996]. Better yet, consult with

a specialist in the area (e.g., an organizational

psychologist) to assist you. Developing a good

questionnaire requires a significant investment

of resources; so whenever possible we suggest

you use existing questionnaires, scales or items.

Administering an employee survey

Devise a method of distributing and collecting

questionnaires so that you will know your

response rate; i.e., how many have been returned

out of the number given to potential respondents.

It is important to achieve high response rates in

surveys so that the results can be considered

representative of the entire group to which the

questionnaires were given. Another check on

representativeness - especially important in the

case of a poor response rate - involves looking

for any differences (e.g., age, department, etc.)

between those who responded to the

questionnaire and others who did not. The

greater the difference between the two groups,

the more cautious you must be in drawing

conclusions from the survey. Sending potential

respondents one or two follow up reminders

about completing the questionnaire is a good

idea. Participation is also more likely if you can

assure people of the confidentiality of their

responses, publicize the survey through the

workplace and obtain support from influential

management and worker representatives.

Chapter 6 Quantitative Measurement

61

1) Do the questions seem applicable to your environment? 

2) Was the questionnaire developed on a similar population in a similar environment or, alternatively,

has its validity in a diverse range of populations/environments been demonstrated?

3) Was a process followed for ensuring that the content of the questionnaire was complete? 

(i.e., were all important aspects of what is being measured included in the questionnaire’s content?)

4) Do the questions measure what your intervention is designed to change? 

5) If you are measuring an intermediate outcome with a questionnaire as a proxy for a final outcome,

has a statistically significant correlation between the proxy and the final outcome measure been

established?

6) Has the sensitivity of the questionnaire been shown by its detection of changes over time, ideally

in response to an intervention similar to yours?

7) Has good “test-retest reliability” of the questionnaire been demonstrated?32

8) Is there a high “internal consistency” among groups of questions forming scales?33

Exhibit 6.1 Questions for assessing questionnaire suitability

32 Test-retest reliability, usually measured by a reliability coefficient, which ranges between 0 and 1, is the consistency of questionnaire scores

on the same group of people given the same questionnaire on more than one occasion. The period between occasions should be long enough

that people forget the answers they gave on the first test and short enough that what is being measured has not changed. This depends on what

is being measured, but is typically 2 weeks to 3 months. A reliability coefficient of 0.8 is considered good; most consider a value of 0.7 to be

minimally acceptable.

33 Internal consistency, usually measured by “Cronbach’s alpha”, is a measure of the reliability of scales. Scores on scales are made up by

combining the scores of answers to a group of related questions. Higher values of alpha show that the questions in the scale are in fact related

and can be considered a scale for measuring a construct. Alpha values between 0.70 and 0.90 are optimal.
6.3.5 Analytical equipment measures

Data collected with analytical equipment will not

serve as final outcome measures for evaluating

a safety intervention, but they might serve well as

good intermediate outcome measures. For

example, to evaluate an intervention involving a

workstation or task redesign to decrease

musculoskeletal injury, you could indirectly

measure changes in biomechanical exposures

indirectly through electromyography of muscle

activity or videotaped task performance.

Validity and reliability of analytical equipment

measures

The major issues related to the use of analytical

equipment are largely those related to

experimental control of the study conditions. You

need to ask: is the instrument being used under

the conditions for which it was intended (e.g.,

temperature)? Are proper calibration and

maintenance procedures being followed? Is there

anything present in the environment that could

interfere with the equipment so that it gives false

readings? Is the equipment operator properly

trained and using standard procedures? Any of

these sources of error could potentially affect

results in either a systematic or random way.

The reliability and validity of measurements

taken with analytical equipment can be improved

by minimizing variation in the operation of the

equipment - both in the environment and in those

operating the equipment. Reliability can also be

improved by taking multiple measurements and

using the average as the data point. However,

the additional cost of taking multiple

measurements has to be balanced with the gains

in reliability realized, especially if the equipment

is not a major source of unreliability in the study.

6.3.6 Workplace audits

Workplace safety audits are another way to assess

safety interventions. They focus on safety

elements upstream of injuries, such as safety

policy, management practices, safety programs,

and, sometimes, workplace conditions. Audits

have been developed by both commercial and

non-profit organizations; and large companies

have even developed in-house company-specific

audits. Sector-specific audits also exist. Often,

they are designed to give qualitative information,

but some yield a quantitative measure or score.

These summary scores can then be used as an

outcome measure in evaluating certain

interventions at the organizational level. 

Validity and reliability considerations when

using workplace audits

Before using an audit, consider the same

questions already raised regarding employee

questionnaires (section 6.3.4). In particular, make

sure that the content of the audit is appropriate,

given the intervention’s goals. If the findings

from the audit are being used as a proxy for a

final outcome measure, such as injuries, you will

need data that validates its use in that manner.

Data could be from similar workplaces and show

a statistically significant correlation between

audit scores and injuries.

6.4 Choosing how to measure the

outcomes

Your choice of outcome measures will depend on

many things, including the nature of the

intervention and its objectives, the setting, and

your resources. While injury rates might be a

suitable choice in one case; it might not be in

another.

6.4.1 Evaluation design and outcome

measures

Final outcome measures

Consideration of the safety intervention’s

objectives should help in deciding what is the

ideal type of outcome to assess the intervention’s

effect. If the intervention is ultimately meant to

reduce injuries in the workplace, then the ideal

outcome measurement is an (unbiased) measure

Quantitative Measurement Chapter 6

62
of injuries. Unfortunately, the frequency of losttime events in a given month or year in many

workplaces is too low to show clearly an

intervention’s effect. Sometimes, inconsistent

biases in the injury statistics are of concern. If

you cannot collect useful injury data, then you

need a good substitute - with evidence that it is

indeed a good substitute. For example, if you

want to evaluate your intervention using

observations as a substitute for injury rates, you

need to show that a strong correlation exists

between the observational measure and

(unbiased) injury statistics. 

Choosing intervening outcome measures

The choice of intervening outcome measures will

depend on an understanding of how the

intervention works, as shown in the conceptual

model or program logic model relevant to your

intervention. We already discussed how you can

strengthen your evaluation by including

measurements of the steps between the

intervention and the final outcome (Section

4.2.5.1). This provides insight into how the

intervention worked (or did not work), which is

useful for planning future interventions. It can

also bolster any evidence of an effect on the final

outcome. For example, you might find that a

decrease in injuries followed a training

intervention. There is a temptation to think that

the intervention had been successful. However,

Chapter 6 Quantitative Measurement

63

Evaluation design and outcome measures 

1. Which measures should be included to address the objectives of the safety intervention (final

outcome)? 

2. Which, if any, measures should be included to provide an understanding of how the intervention

works or bolster the strength of the design (intermediate and implementation outcomes)?

Measuring unintended outcomes

3. Which measures should be included to detect possible unintended outcomes of the intervention?

Characteristics of measurement

4. Do the methods really measure the outcomes they are intended to measure, from a conceptual

point of view (construct validity)?

5. Is the outcome measurement method free of systematic biases (validity)?

6. Is the measurement method reliable?

7. Have the measurement methods been used on a group similar to the one under study before?

Statistical power and measurement method

8. Will there be sufficient statistical power during analysis with the method chosen and the number

of evaluation participants?

Practical considerations

9. Is the measurement method feasible (i.e., cost, administrative requirements)?

Ethical aspects

10. Can the measurements be carried out in an ethical manner (i.e., fully informed consent)?

Considerations when choosing the outcome measures
if you also measured the practices targeted by the

intervention and found that they did not change,

the question arises as to whether the change in

injury rate was due to something else besides the

intervention. On the other hand, if both injuries

and unsafe practices showed a decrease

following the intervention, you could be more

confident that the intervention indeed caused the

cause of the decrease in injuries.

A thorough effectiveness evaluation determines

the extent to which the intervention was

implemented as planned. This information will

be especially valuable if the intervention appears

to have no effect. You want to distinguish

between the two possibilities: 1) the intervention

is inherently ineffective, even when implemented

as planned; or 2) the intervention is potentially

effective, but was poorly implemented. Such

information is valuable to those who might want

to repeat the intervention or who design

interventions. Program implementation can be

assessed using both qualitative and quantitative

measures.

6.4.2 Measuring unintended outcomes

Unintended consequences of the intervention, by

their very nature, are difficult to anticipate, and

hence, difficult to measure. It is possible that an

intervention successfully decreases one type of

injury but increases another type. This increase

could occur in the same group of personnel or it

could involve another group within the same

workplace. Safer conditions, for example, for

equipment operators might mean more danger

for maintenance workers. The basic principle in

measuring unintended outcomes is to include

measurements apart from the ones most directly

related to the intervention. 

Other unintended outcomes may arise through

compensatory behavior in response to the

intervention. A particular engineering

intervention to reduce exposure to a hazard, for 

instance, could result in a decrease in the use of 

personal protective equipment because people

feel safer. By including a measure of personal

protective equipment use in your evaluation, one

could see if this was happening. If so, it could

explain why an intervention which looked

promising failed.

6.4.3 Characteristics of measurement method

We already discussed the very important

considerations of reliability and validity at the

beginning of this chapter. You also need to

consider these characteristics of the measurement

method within the context of the group and

setting where it is applied. For example, a

questionnaire developed to be reliable and valid

with a white-collar, native-speaking working

population could perform poorly with a bluecollar, immigrant population. Thus,

measurement methods developed with a

different work population might need

modification before they can work well in

another situation.

Consider also the conditions under which the

Quantitative Measurement Chapter 6

64

An example of unintended outcomes

measurement

Interventions to decrease needlestick injuries

in hospitals have typically involved

recommendations to avoid recapping. The

primary indication of success of this

intervention is a decrease in the frequency of

recapping injuries. However, it has also been

important to track other types of needlestick

injuries. In some cases an increase in injuries

during disposal has been detected, which has

led to replacing disposal receptacles with

ones of a safer design. You also need to

confirm that the decrease in needlestick

injuries in health personnel has not been

achieved at the expense of an increase in

injuries to those who handle disposal

receptacles and garbage.
measurement method is used. If they are not the

same as those for which the method was

designed, then determine whether they perform

well under the new conditions. A delicate

instrument performing well under laboratory

conditions might not do so well in a workplace

where there is vibration, dust, etc. The results

from a self-administered questionnaire could be

quite misleading if, because of workplace politics,

you are not allowed to ensure that everyone has

actually received the questionnaire. Such issues

of appropriateness and the implications for

reliability and validity of data might lead you to

choose a different measurement method than

what might be used under other conditions.

6.4.4 Statistical power and measurement

method

In choosing an outcome measure, consider

whether there will be sufficient statistical power

during analysis (see section 8.4). Thus, a power

calculation should be carried out before the

intervention is implemented. Calculations might

show that the outcome measure initially chosen

will not yield sufficient power, given the planned

number of evaluation participants. You might

then choose a different measurement method or

measure a different outcome in order to increase

power. For instance, you might decide to use a

self-reported symptom survey or reported minor

injuries instead of reported lost-time injuries. 

6.4.5 Practical considerations 

It is also important to be practical when choosing

measurement methods. What is the cost of

taking these measurements in terms of time and

material resources? How much disruption of

work processes is involved in taking these

measurements? Is the necessary expertise

available to carry out these measurements

properly? Are data already being collected for

other reasons available for the purposes of the

evaluation?

6.4.6 Ethical aspects

There might be ethical issues about the use of

some measurement methods. For instance,

behavioral observations may be inappropriate in

some environments - at least without the consent

of those being observed. It is customary, actually

required, that researchers in an academic

environment obtain written consent from

participants before using personal data (e.g.,

health records, employee opinions).

6.5 Summary

This chapter highlighted two important

measurement concepts: reliability and validity.

Several methods of measuring safety outcomes,

including administrative data collection,

behavioral and work-site observations, employee

surveys, analytical equipment measures and

workplace audits were reviewed with a focus on

reliability and validity issues. Additional issues

which influence the choice of evaluation

measurement methods besides measurement

properties were also discussed: outcomes

indicated by the evaluation design; detecting

unintended outcomes; statistical power;

practicality; and ethics.

Chapter 6 Quantitative Measurement

65
Quantitative Measurement Chapter 6

66

Key points of Chapter 6

• Choose implementation, intermediate and final outcome measures based on the intervention’s

conceptual model or program logic model, as well as the objectives of the intervention.

• Consider injury statistics, other administrative records, behavioral/work-site observations,

employee surveys, analytical equipment and workplace audits as means of measuring outcomes.

• Use measurement methods which are valid, reliable and practical.

• Try to eliminate bias in injury statistics or keep such bias constant. If there is change, report on its

estimated effect on the results.

• Choose measures which will yield sufficient statistical power during analysis.

• Consider the ethical aspects of measurement methods.

• Anticipate and try to measure unintended outcomes of the intervention.
67

Qualitative methods for

effectiveness evaluation:

When numbers are not enough

Chapter7

7.1 Introduction

7.2 Methods of collecting qualitative information

7.2.1 Interviews and focus groups

7.2.2 Questionnaires with open-ended questions

7.2.3 Observations

7.2.4 Document analysis

7.3 Using qualitative methods in evaluation

7.3.1 Identifying implementation and intermediate outcomes

7.3.2 Verifying and complementing quantitative outcome measures

7.3.3 Eliminating threats to internal validity

7.3.4 Identifying unintended outcomes

7.3.5 Developing quantitative measures

7.4 Selecting a sample for qualitative studies

7.5 Qualitative data management and analysis

7.6 Ensuring good quality data

7.7 Summary
7.1 Introduction

Qualitative methods play an important role in

safety intervention evaluation. Although in most

situations, numbers are necessary to prove

effectiveness, qualitative methods can yield

information with a breadth and depth not

possible with quantitative approaches. 

We first describe four methods of gathering

qualitative information: 1) interviews and focus

groups; 2) questionnaires with open-ended

questions; 3) observations; and 4) document

analysis. We identify and illustrate several

different ways in which these types of data can be

used in an effectiveness evaluation. We follow

with some details of how to select study subjects,

analyze the collected data, and ensure good

quality data. 

7.2 Methods of collecting qualitative

data

7.2.1 Interviews and focus groups

A major means of gathering qualitative

information is through in-depth interviewing.

This involves open-ended questions, where

interviewees can answer questions on their own

terms and in as much detail as they like. This is

in contrast to the typical questions found on

employee surveys, that prompt for yes/no,

multiple choice or very short answers. For

example, a truly open-ended question asks “what

do you think about the new safety program?”.

In contrast, only a limited range of answers is

allowed if you ask, “how useful was the new

safety program?” or “was the new program

useful?”

The types of questions used in interviews will

depend on the purpose of the data- gathering.

They could be about any of the following: 

• knowledge (e.g., What did you learn about in

the training?) 

• experience (In what ways, if any, have things

changed in the way safety is done around

here, since the program began?) 

• practices (In what way, if any, has the training

program influenced your safety practices on

the job?) 

• opinions (What do you think of the

program?) 

• beliefs (What do you think the company’s

goals are in providing you this program?) 

• feelings (How do you feel about participating

in the program?). 

A good interviewer is sensitive to the mood and

feelings of the interviewee(s), listens well, and

encourages them to elaborate on the topic

discussed. Better interviews will result from

someone who has been trained to conduct

interviews and has practiced with the interview

questions. There are a number of approaches for

collecting interview data. 

Structured interviews

Structured interviews contain a standardized

means of getting information. The same set of

carefully worded and ordered set of questions

are used with each respondent. This technique

reduces the level of skill required for the

interviewer to do a good job and curtails the

influence of any particular interviewer on the

results. Structured interviews are useful where

several people are conducting the interviews or

if the interviewers are inexperienced. On the

other hand, there is less opportunity to learn

about individual subject differences and

circumstances while using the structured

approach.

Qualitative Methods Chapter 7

68

Methods of collecting qualitative data

1) Interviews and focus groups 

2) Questionnaires with open-ended questions

3) Observations 

4) Document analysis
Semi-structured interview

A semi-structured approach to interviewing

represents a compromise between

standardization and flexibility. Here, an

interview guide is used, which is basically a

checklist of the issues explored during the

interviews. There is no set order to the topics,

and specific questions are not necessarily worked

out ahead of time. However, before ending the

interview, the interviewer makes sure all the

items have been covered, through the natural

course of the conversation. Any topics not yet

covered can then be addressed. As with the

structured interview, this method ensures that

the same type of interview data are gathered

from a number of people. 

Unstructured interview

The unstructured interview is more like an

informal conversation, where questions are

generated during the natural flow of

conversation. Although certain topics are

covered, there are no predetermined questions.

The data varies with each person interviewed.

This makes the analysis more challenging. As

well, more opportunity exists for an interviewer’s

bias to influence the results. The strength of this

approach though is that the interviewer can tailor

the approach and line of questioning to each

individual.

Focus group interview

A focus group is like an interview with a small

group of people rather than only one person. A

semi-structured approach is most useful. About

six to ten people can be interviewed together and

the interviews usually last from one-and-one-half

to two hours. This allows time for participants to

discuss about eight to ten questions.

The focus group technique is a highly efficient

way to collect data. You receive the opinions of

several people at the same time. The social

setting provides a measure of validation for the

information, since extreme or false views tend to

be challenged by others in the group. A skilled

facilitator can guide the group’s dynamics so that

the participants stay on topic and people who are

either shy or have less popular opinions are

encouraged to speak. 

Exert some caution in selecting individuals for a

focus group. First, this format is not advisable if

sensitive information of either a personal or

organizational nature is sought. People might be

reluctant to speak up and could be vulnerable to

repercussions if they do. For similar reasons, and,

depending on the subject of the interview, you

should probably group people together with

similar positions within the organizational

hierarchy. In particular, consider separating labor

and management; and supervisors and those

they supervise. In some cases, you might want to

group men and women separately.

Chapter 7 Qualitative Methods

69

1. Let the subject(s) know at the outset how long

the interview will last, its purpose and general

outline. Explain how confidentiality will be

observed.

2. Obtain consent (preferably by signing a consent

form) for participating before starting the

interview

3. Start off the interview with non-controversial

questions that require minimal recall. More

sensitive topics, including questions on

knowledge, should be covered once a rapport

has been established.

4. Create an atmosphere of having a conversation.

You do not want people to feel as if they are

being examined.

5. Ask clear, truly open-ended, questions.

6. Be nonjudgmental.

7. Be attentive. Indicate interest through your

actions and offer verbal feedback.

8. Tape record the interview in order to have a

detailed record for analysis. Record important

points in your notes.

Guidelines for obtaining good interview

data
7.2.2 Questionnaires with open-ended

questions

Researchers do not consider structured

questionnaires - even with truly open-ended

questions - to be the most effective way to gather

qualitative information. It is assumed that many

people do not want to take the time to write out

a response. As well, it cannot be sensitive to

interviewee differences, since everyone gets the

same question. The depth of responses is limited

because there is no opportunity to follow up on

an interviewee’s statement with other questions. 

On the other hand, if you are using a

questionnaire to measure the quantitative

objectives in the project, you can then quite

economically expand the breadth of the results

by including a few open-ended questions. These

can be useful for gauging participant reactions,

identifying program barriers, bringing out

unintended consequences of the intervention,

and verifying the picture obtained from

quantitative measures. Furthermore, the results

of this initial screen can help you decide on the

nature and extent of any follow-up qualitative

studies.

7.2.3 Observations

Another way of collecting qualitative data is to

actually go on-site and observe what is going on.

Depending on your needs for the evaluation,

everything can be captured, including the

physical environment, social organization,

program activities, as well as behaviors and

interactions of people. Or you can take a more

narrow focus. The type of observational data

used in qualitative analyses can be different than

that used in quantitative analyses. In the latter,

specific observations are always being sought:

e.g., whether a particular procedure is being

done correctly or if a particular work-site

condition is observed. In contrast, for the

purpose of qualitative analysis, specific types of

observations might not be defined beforehand.

Observational data is especially helpful in

evaluating safety programs as an external

evaluator. An understanding of the physical and

social environment will be increased. You will

catch issues that might go unreported during the

interviews because the insiders are too close to

their situations. As well, people might not speak

freely during interviews in fear of reprisal from

co-workers or management. Finally, an on-site

visit can be the best way to verify that

intervention activities are occurring as described.

If you are an internal evaluator planning to use

observations, be aware that one’s view of things

is influenced by one’s background and position

within the organization. Thus, if observations

are going to play a large role in an evaluation,

consider bringing in an external, more neutral

observer. Similarly, you might have to choose

between being an observer or a participant, or

something in between. The more you participate,

the more first-hand your knowledge will be. The

disadvantage is that it becomes more difficult to

maintain “objectivity” and your presence could

influence those around you. 

Tailor the length and frequency of observations to

your requirements. This can range from a single

two-hour site visit to verify program

implementation to a full-time, year-long presence

to fully understand, for example, a change in

safety climate. Field notes are the primary means

of recording observational information. This can

be supplemented with photographs or videos,

although such methods are often obtrusive.

Good field notes require a selectivity that can

focus on the important details, yet not severely

bias the notes.

7.2.4 Document analysis

Documents of interest in workplace safety

intervention evaluations can include material

containing policies or procedures related to the

intervention, safety records, committee minutes,

correspondence, memoranda, or reports. They

can suggest topics to include in interviews or

Qualitative Methods Chapter 7

70
questionnaires and offer evidence of intervention

implementation, barriers to implementation, or

other events in the workplace that could threaten

the evaluation’s internal validity.

Be aware that documents are never more than a

partial reflection of reality. Some are normative;

such as procedures documents. They tell what

should be done, not whether it actually is done.

Some documents are descriptive - e.g., minutes

of meetings. However, they can reflect one

person’s view (e.g., the minute-taker or chair of

the meeting), more than the collective view.

7.3 Ways to use qualitative methods in

effectiveness evaluation

Interviews, questionnaires, observations and

documents are used alone or in combination

towards several purposes in safety intervention

evaluations. Here, we elaborate on five ways in

which they can contribute to an effectiveness

evaluation. 

7.3.1 Identifying implementation and

intermediate outcomes

Qualitative data can help elucidate the steps

between the intervention and the final outcome,

including implementation and intermediate

outcomes. They can identify results not captured

in the quantitative measures. This can be an

important addition to an evaluation, since it is

not usually possible to quantitatively measure

every pertinent intermediate effect of the

intervention. It can be difficult to anticipate them

all and measure them quantitatively. You

especially want to find out the extent to which

the intervention was implemented as planned.

Document analysis, observations and interviews

can be used to check on program activities.

7.3.2 Verifying and complementing

quantitative outcome measures

Qualitative measures are used to verify

quantitative measures. Through an approach of

“triangulation”, two or more different

methodological approaches can measure the

same thing in order to establish consistency. You

Chapter 7 Qualitative Methods

71

Ways to use qualitative methods in

effectiveness evaluation

1. Identifying implementation and

intermediate outcomes

2. Verifying and complementing quantitative

outcome measures

3. Eliminating threats to internal validity

4. Identifying unintended outcomes

5. Developing quantitative outcome

measures

Example of how qualitative methods can

be used to identify intermediate outcomes

Let us return to an earlier example34 where an

intervention consisted of a workplace- based

incident investigation team assisting

supervisors in their investigation of incidents.

Quantitative data included final outcome

measures (frequency and severity of injuries)

and some intermediate outcome measures

(length of time between incident and its

report and percentage of incidents generating

corrective action proposals). Interviews

helped fill in the picture further of how the

intervention could have led to the observed

decrease in injuries and their severity. The

interviews revealed that supervisors and

safety representatives found the incident

investigation teams helpful and felt that better

corrective actions were conceived. Thus,

better quality corrective actions - an

intermediate outcome - has been identified as

a plausible means by which the frequency

and severity of injuries were decreased.

34 Menckel and Carter [1985]
might undertake a broad-based safety initiative

to change the “safety climate” in the workplace.

Certainly, you could use a safety climate

questionnaire, which typically consists of closeended questionnaire items, to assess a change in

safety climate. Also valuable are open-ended

questionnaire items or interviews completed by

key personnel regarding observed changes in the

workplace atmosphere concerning safety. If the

methods are consistent in their portrayal of

change in safety climate, then a “crossvalidation” of the methods has been achieved

and you can present your conclusions with more

confidence. 

Sometimes the methods are complementary in

that they might measure different aspects of the

same concept. Open-ended questions or

interviews might detect aspects of change missed

by a questionnaire containing only close-ended

items. 

7.3.3 Eliminating threats to internal validity

Interviews with key officials can provide

information crucial for addressing potential

threats to internal validity. 

7.3.4 Identifying unintended outcomes

Interviews and, possibly, observations are useful

ways to identify unintended outcomes.

Although some unintended outcomes can be

assessed quantitatively, such as an increase in an

untargeted type of injury, others would be better

detected through qualitative inquiry.

Interviews are an especially good at gauging the

reactions of intervention participants and others

involved in the intervention, including

supervisors, union leaders and managers. Their

reactions and those of others involved with the

intervention, are important, since a poor

response by an influential individual or group of

individuals at a work-site could have a big effect

on the program. It might explain the lack of

success of a promising intervention. Unintended

outcomes can also be more positive. In one

evaluation, for example, interviews with workers

and foremen showed that several people believed

that the recent decrease in the number of labor

grievances could be attributed to the improved

industrial relations resulting from the

participatory ergonomic program. 

7.3.5 Developing quantitative measures

Data collected using qualitative methods in the

planning stage of the evaluation can provide the

basis for the subsequent development of relevant

quantitative measurement instruments. Here are

three examples. 

Qualitative Methods Chapter 7

72

Example of how qualitative information

helps reduce threats to internal validity

In the evaluation example just discussed on the

previous page, interviews and analysis of safety

committee minutes revealed the following

information which helped eliminate threats to

internal validity. The workplace physical plan,

products, production techniques and activities, as

well as the safety-related policies, purchases and

activities (apart from the creation of the incident

investigation committee) had remained constant

over the six-year evaluation period - suggesting

no evidence of history threats. There was also no

evidence for an instrumentation or reporting

threat, since there were no changes in the incident

reporting criteria, nor in safety-related policies,

purchases and activities (apart from the creation of

the committee).
7.4 Selecting a sample for qualitative

purpose

Once you have decided to use qualitative data

collection methods as part of the program

evaluation, you need to decide from whom, or

about what, data should be collected. This might

include collecting data from specific employee

work groups, manager groups, female or male

workers, or different classifications of workers.

Additionally, you might want to collect data

about a particular event, occurrence, or incident.

Rather than surveying the entire work force, use

what is called purposeful sampling. Here, one

selects information-rich cases to study in-depth.

They are purposefully selected so that the

investigator can learn, in detail, about issues of

central importance to the program. For example,

you might want to ask different employee

workgroups about their experience in a particular

occupational safety program. Then compare

quotes across groups to see if there are differences

in experiences which might influence the

intended goals of the program. Furthermore, you

might separately ask male and female workers

about any problems in participating in the

program. Again, comparisons can be made to

see if both females and males similarly received

the program as intended. 

We describe eight different purposeful sampling

strategies that may be used.

Extreme or deviant case sampling 

Identify unusual or special cases. It is possible

that much can be learned from extreme

conditions (good or bad) rather than the many

possibilities which fall in the middle. For

example, survey data collected after a safety

program is over might show one or two people

Chapter 7 Qualitative Methods

73

Examples of how qualitative studies can help develop quantitative instruments

1) Interviews, observations and document analysis can lead to the development and inclusion of

certain items on questionnaires. For example, say that opinions expressed in interviews had a

repeating theme that safety is for sissies. If your intervention is in part designed to change this

attitude, then it would be a good idea to develop a questionnaire that includes questions which

measure such safety attitudes.

2) People have used the details of incident records, a qualitative information source, to develop

workplace-specific checklists of work practices or work-site conditions used in quantitative

assessment. They review records to find which unsafe practices and conditions are associated with

incidents. Interventions are then developed which encourage the practice of safer alternatives. As

well, checklists of these safe practices and work-site conditions are developed and used in

evaluation. Quantitative measurement consists of making (random) observations and recording

whether the safe or unsafe version of the practice or work-site condition was observed.

3) Menckel and Carter35 described a new safety initiative in which a group assisted workplace

supervisors in their investigation of incidents within their division. Preliminary interviews and

document analysis showed that there was often a long delay between incident occurrence and its

formal reporting. As a result, corrective safety measures were correspondingly delayed in their

implementation. Thus, one of the ways evaluators chose to measure the effect of a new workplace

incident investigation group was by how long it took for incidents to be reported. 

35 Menckel and Carter [1985]
who have made big changes. A follow-up with

an interview could validate the responses as well

as discover what in the program motivated them

to make such big changes. By limiting the focus

to extreme cases, this approach to sampling is

economical in time and resources.

Heterogeneity sampling/maximum variation

sampling

Identify cases with differing characteristics (e.g.,

age, gender, education, job classification) to

provide diverse points of view. Any common

patterns emerging from the variant cases can

capture the core experiences and shared aspects

of a program or event. 

Homogenous sampling 

Identify a small group of information-rich cases

- similar in terms of background, employment

level, experiences, etc. and explore the issue of

interest in depth. It might be of interest to

separate groups of management and then labor

and compare their opinions about a safety

program.

Typical case sampling 

Identify “typical” individuals to describe the

benefits of the program. Cases are selected with

the co-operation of key informants such as

program staff. This information can be used to

help “sell” the program to others reluctant to

participate.

Critical case sampling 

Find individuals who could dramatically make a

point about the program. They may be identified

by asking a number of people involved with the

program. A good bet are the leaders in the group

who could provide suggestions about how to

improve the program.

Criterion sampling 

Identify and study cases that meet some

predetermined important criterion. Even if all

employees at the work-site receive the training,

you might interview only those most exposed to

the particular hazard targeted by the training.

They may reveal major system weaknesses that

could be targeted for improvement.

Politically important case sampling 

Identify, and select (or not) politically sensitive

individuals. You might want to interview a

union steward who supports the program, and

thereby can enrich the information obtained.

Convenience sampling 

The most common method in selecting

participants for qualitative data collection lies

with picking cases that are easiest to obtain and

those most likely to participate. This is also the

least desirable method. The problem is that in

the end, it is difficult to know exactly who was

interviewed and if their opinions are consistent

with others possibly affected by the program.

7.5 Qualitative data management and

analysis

A variety of methods are used to analyze

qualitative data. The process is described here

in very general terms and appears as a sequence

of steps, which in actual practice can occur

simultaneously or may even be repeated. First,

all raw information, if not already in a written

form, is converted to text. Thus, taped interviews

are transcribed and visual material is

summarized using words, etc. This body of

textual material is reviewed to identify important

features and, possibly, summarize them. A

coding system of keywords, or some other data

reduction technique, is developed to facilitate this

process. The data, either in summarized form or

not, is then reviewed to identify patterns. These

Qualitative Methods Chapter 7

74
patterns are concerned with the following:

similarities or differences among groups or

events; repeated themes; and relationships

among people, things or events. 

Identification of patterns leads to some

generalizations or tentative conclusions

regarding the data. Depending on the scope of

the investigation, you might examine the

trustworthiness of these generalizations by

testing them with the results of further data

collection or comparing them with existing

theory. 

Success at the data analysis stage requires that

good data management practices are observed

from the beginning of data collection. Use

systematic methods for collecting, storing,

retrieving and analyzing data. People have

developed various techniques to help highlight,

organize or summarize data. A useful reference

in this regard is the book by [Miles and

Huberman 1994]. This reference also reviews the

various software developed to assist in both the

data reduction and pattern recognition stages of

analysis.

7.6 Ensuring good quality data

Concerns about reliability and validity apply to

qualitative data, just as they do to quantitative

data. Thus, anyone reading a report of a

qualitative investigation wants to know that the

stated methods have been used consistently

throughout the study (reliability concerns). They

also want to know that there are no hidden biases

in the data collection, the data analysis nor the

conclusions drawn (validity concerns).

The following contains considerations and

suggestions for ensuring that good quality data is

collected.

Minimizing evaluator bias 

The product of a study no doubt bears the

personal mark of the people conducting it.

However, researchers generally try to reduce

their effect on their research by using concepts

and methods agreed upon by other researchers.

Ways to guard against bias include the following:

outlining explicit methods for data collection and

data analyses; adhering to these methods;

having more than one researcher collect data;

having a second, non-biased person summarize

and/or draw conclusions from the data; and

letting the data speak for themselves and not

forcing them into a framework designed by the

researcher.

Appropriate sampling

Someone reading your evaluation wants to be

sure that the right sample has been selected for

the stated purpose. For example, you could not

claim to be truly representing workplace

perceptions of the effectiveness of an

intervention, if either management or employee

representatives are not represented. Thus, the

rationale and method of sampling must be

explicit and justified with respect to the study’s

aims. 

Validation by subjects

One of the best ways to determine whether or

not you “got it right” in your study, is to check

with the subjects you are studying. This involves

confirming the accuracy of the data collected, the

reasonableness of the method used to summarize

it, and the soundness of the conclusions. Of

course the potential biases of the subjects

consulted must be kept in mind when weighing

their opinions.

Thorough methods of drawing conclusions

Avoid drawing conclusions too soon. This can

be caused by researcher bias or pressure to come

up with answers quickly. In contrast, wellgrounded conclusions require time for at least

some of the following activities: 1) reviewing

collected data to identify anything which has

been overlooked; 2) searching for evidence which

Chapter 7 Qualitative Methods

75
contradicts preliminary conclusions, either by

reviewing data already collected or by gathering

new data; 3) confirming important data or

conclusions through “triangulation”, i.e., finding

agreement when using a different data source,

methodology or researcher; and 4) exploring

alternative explanations for patterns observed in

the data.

Conduct a pilot study

Conducting a pilot study or trial run with your

proposed research methods is often of great

value. Feedback from those involved in the pilot

study can be used to refine a sampling strategy,

interview guide, other data collection procedures,

and even procedures for data management.

7.7 Summary

We have reviewed four major methods for

gathering qualitative information: interviews;

questionnaires with open-ended questions;

observations; and document analysis.

Qualitative data can be used in several ways to

complement quantitative methods: identifying

implementation and intermediate outcomes;

verifying and complementing quantitative

outcomes; eliminating threats to internal validity;

identifying unintended outcomes; and

developing quantitative measures. In contrast to

quantitative methodology, qualitative methods

usually employ one of several purposeful

sampling strategies. We briefly discussed

methods of analysis and methods to ensure good

quality data.

Qualitative Methods Chapter 7

76

• Use interviews and focus groups, questionnaires with open-ended questions, observations, and

document analysis to enrich your evaluation.

• Use qualitative methods for one or more purposes:

• identify implementation and intermediate outcomes

• verify and complement quantitative measures

• eliminate threats to internal validity

• identify unintended outcomes

• develop better quantitative measures. 

• Use one of several purposeful sampling strategies.

• Collect and analyze data in ways which enhance their reliability and validity.

Key points from Chapter 7
Chapter 7 Qualitative Methods

77

79

Statistical Issues:

Are the results significant?

Chapter8

8.1 Introduction

8.2 Why statistical analysis is necessary

8.3 P-values and statistical significance

8.4 Statistical power and sample size 

8.5 Confidence intervals

8.6 Choosing the type of statistical analysis

8.6.1 Type of data

8.6.2 Evaluation design

8.6.3 Unit of analysis

8.7 Avoiding pitfalls in data analysis

8.8 Summary
8.1 Introduction

This chapter will not answer all your questions

on statistics. It cannot cover all the possible

approaches that intervention evaluations might

require. Statisticians will maintain they should be

consulted right from the design stage of a project.

This is not just self-interest. Certainly, they want

your business - including the consultation fee!

But even the statistician among us (HSS), who

typically provides free consultations for faculty

colleagues, makes the same point: there are often

aspects of the way the evaluation is designed, or

the type of data collected among other factors,

that mean the statistical analysis will not be

entirely straightforward. You can avoid ending

up with “messy data” by discussing the study in

advance. The data could still turn out to be

complicated and it may be best to find a

statistician to do the analysis. After all, you have

probably spent a lot of resources on ensuring the

highest quality of intervention and data

collection; so you do not want a second-rate

evaluation.

This chapter provides an overview of the

statistical concepts applicable to intervention

evaluation. We start by explaining the need for

statistical methods, followed by a discussion of

the meaning of p-values. If you have ever read a

scientific paper with quantitative information,

then you have seen p-values. They show an

equation like “p<0.05” along with a comment

stating if the result is “statistically significant”.

Another way of presenting statistical results are

confidence intervals. Also being introduced is the

notion of statistical power and how that relates to

the sample size. 

Later in the chapter, we discuss what issues to

consider in choosing a statistical technique. Two

have already been mentioned - the type of data

you have and the study design being used. No

calculations are shown in this chapter, but some

simple examples are included in Appendix B.

They correspond to the evaluation designs

outlined in Chapters 3 and 4. 

8.2 Why statistical analysis is

necessary

Surely, if the change in injury rate in an

intervention group is greater than the change in

injury rate in the comparison group, doesn’t that

prove that the intervention has worked? Why

are statistics needed? The answer is that real-life

data are subject to random variability. Suppose

you have a perfectly balanced (“fair”) coin.

(Statisticians love using examples about cointossing to explain the principles they use.) Toss it

ten times, and you can expect five heads and five

tails. But it is also reasonably likely that you

could get six tails and four heads, or four tails

and six heads simply as a result of chance

(random variability). You might also get a 7-3

split. As will be seen in the next section, the

question from a statistical viewpoint becomes:

how far from a 5-5 split do I have to get, before I

become suspicious about the coin and question if

it really is fair?

The analogy with the safety situation can be seen

if we think about a study investigating whether

back belts reduce back pain. You randomize half

the people to receive back belts (the intervention

group), while the other half (the control group) is

left alone. After the intervention group has had

back belts for a while, everyone is asked about

levels of back pain. [This is an example of an

experimental design with “after”-only

measurements, Section 4.3.2] For each person,

there is a pain score. 

The average score in the group given back belts

may be somewhat better than the average in the

control group. Does this mean that back belts

work - or is it that simply by chance, the

randomization led to more people who have a

lot of back pain ending up in the control group?

And what if it is the opposite? Suppose, the back

belt group does a little bit worse than the control

group? Does that mean that these belts are

actually harmful - or is it because there happened

to be more people who get pain in the

intervention group? Statistical analyses can

Statistical Issues Chapter 8

80
indicate how likely (probable) these possibilities

are. 

Statistical techniques can also address a selection

threat to internal validity, i.e., when differences

in participants’ characteristics between the

intervention and control group could be

responsible for the measured intervention effect

(Section 4.4.1). You notice, for instance, that

people given back belts are on average somewhat

older than those who do not get them.

Furthermore, because older workers are less

likely to use the belts, and the intervention group

itself is older, you might not see much change in

comparison with the control group. To reduce

this type of threat, statisticians have developed

techniques that account for or control the

difference in ages (or other variables) between

the two groups.

8.3 P-values and statistical

significance

A leading philosopher of science in the 20th

Century, Sir Karl Popper, argued that science

proceeds by the method of refutation. At any

time, scientists have only the best theory (or

hypothesis) at the moment to describe how the

real world works. This hypothesis can always

change based on new observations. What

scientists must do, argued Popper, is to devise

experiments aimed at disproving (refuting) their

latest theory. As long as the experiments fail to

do so we continue to regard the theory as at least

a reasonable approximation to the real world. If

an experiment disproves the theory, then a new

one must be adopted. Classical statistical

reasoning works in a similar fashion, basing the

rejection of an initial hypothesis on probabilistic

grounds.

With our example of back belts: start from a

position of skepticism about their value, i.e.,

hypothesize that the intervention has no effect

(null hypothesis). If the program is useless, then

expect no difference in the back pain between the

intervention and control groups. However, in

Chapter 8 Statistical issues

81

What do we mean by a “true”effect?

Several times in this chapter we refer to a

“true” or “real effect” of a program or

intervention. Surely, you may think, the true

effect is what we find. How could the effect

be considered not true?

Part of the answer is that the estimate of the

effect is subject to variability. The groups

studied may be comparable, but cannot be

identical even if they are created through

randomization. So if you repeat your

evaluation study elsewhere the size of effect

might be larger or smaller.

If you repeat the study many times, you could

take the average (mean) of the effect sizes.

This would balance out the times when the

effect just happens to be larger with those

when it happens to be smaller. In practice,

studies are rarely repeated even once, let alone

many times. But you can do this as “thought

experiment”. In fact, statistically we think

about a (hypothetical) infinite number of

replications. If we could actually do them, the

average effect size over the replications would

be what we have called the true effect.

Caution: Having emphasized the vital

importance of statistical analysis, we warn

you about indiscriminately using statistical

packages. Inexperienced researchers are

sometimes tempted to feed their data into a

standard software package and ask for

everything to be compared with everything

else. This is not good practice. Statistical

testing should follow a clear definition of

hypotheses; and the testing should not

determine the theory. Instead, the hypotheses

should come from the chosen intervention

models.
practice, the intervention group sometimes does

better and sometimes worse than the control

group, i.e., the average scores show less pain or

more pain. The question then becomes: how big

a difference must exist between the groups before

you start to doubt the null hypothesis and accept

that the change comes from a real effect of the

program? 

Typically, the statistical approach takes into

account the difference in the mean (average)

levels of pain between the two groups, as well as

how much variability exists between the scores of

the people in the study and the sample size (how

many people are included in the study). The

analysis produces a p-value, which can be

interpreted as:

When this probability is small enough, you reject

the hypothesis of no difference and start to

believe (at least for practical purposes) that the

back belts have changed the level of pain. When

the p-value is larger, you cannot reject the

hypothesis, so you would conclude the belts do

not “work”, at least in the way they were used.

The cut point for the p-value, which represents

the probability you are willing to allow of

concluding the intervention works - or does harm

- when it is really ineffective,36 is known as (the

Greek letter alpha). When the p-value is less than

this, the result is declared statistically significant.

How small does the probability have to be for

you to reject the hypothesis and claim that the

intervention works? Strictly speaking, there is

no right or wrong answer here. It depends on

your willingness to draw the incorrect conclusion

that the belts work when they really do not. This

in turn depends on the resource and policy

implications of the evaluation results. The more

expensive the intervention, the less likely you

want to make this type of mistake, so you want

the probability to be very low; and vice versa - if

the intervention is cheap and aimed at very

severe injuries, you may be willing to apply it

even if the evidence of its value is less strong. In

practice, though, alpha is usually taken as 0.05

(or 5%).

8.4 Statistical power and sample size 

Now there is another side to all this. We have

discussed the p-value based on the condition that

the program is useless. But what if it works? If

the intervention is truly effective, you want to be

reasonably sure to reject the initial null

hypothesis. Just as you can get six heads and

four tails even with a fair coin, you could also get

five heads and five tails even with a coin biased

toward heads. Similarly, even if the program

truly has a moderate effect, you might be unlucky

in your study and only observe a very small

difference, which may not be statistically

significant. If you fail to reject (i.e., you accept)

your initial hypothesis of no difference, and there

really is one, the mistake is known as a Type II

error. The probability of such a mistake, i.e., the

probability that you fail to reject the hypothesis

when it is false, is known as  (the Greek letter

beta).

This means that the probability that you correctly

reject a false hypothesis, i.e. you detect the

program’s effectiveness, is 1-, and this value is

known as the power of the study. The importance

of this is that you obviously do not want to do a

The probability that a difference at least as

large as the one seen could have occurred

simply by chance, if there really is no effect

of the intervention. 

Statistical Issues Chapter 8

82

36 This type of mistake is known as a Type I error

Important note: In the interpretation of the

p-value, the phrase “if there really is no effect

of the program” is crucial. Ignoring it has led

to many a misinterpretation of p-values. We

now discuss the situation where there is an

effect.
study that has little chance of demonstrating a

real effect of an intervention. You want to be

reasonably sure that you will conclude there is a

difference if one really exists. Thus, it is important

to consider power before undertaking the intervention

and evaluation.

You can do this in two ways. You could set the

power you want and then calculate the sample

size needed; or you may have a certain number

of workers who could be involved in a study, and

you can estimate the power the study would

have with that number. 

The first approach is actually a preferable way to

conduct an evaluation - indeed, clinical trials of

new drugs do it this way round. Typically,

researchers design evaluations so that the power

is 80% (sometimes 90%); that is, if the

intervention is truly effective, there is an 80%

(90%) chance that the data you gather and the

statistical test you use allows you to conclude

that the intervention is effective.

In practice, workplace interventions usually

involve a fixed number of employees, for

example, all workers in a plant or a department.

So you can’t set power in advance - rather, you

should check what power you will have. Several

components go into the calculation of power: the

effect size - how much effect you think the

intervention will have (or should have in order to

be worth replicating elsewhere); sample size (the

number of evaluation participants or, more

formally, experimental units); how much

variability there is between the outcome

measurements within the sample; and the values

you set for and . The formula you use to

calculate power, like your choice of statistical test,

depends on the experimental design and type of

data collected.

All other things being equal, the larger the

sample size, the larger is the power. Similarly,

the less variation in the outcome measure, the

larger the power. If you should find that the

intended plan would likely yield power much

lower than 80-90%, you might want to change

your evaluation design, choice of outcome

measures, or number of people included in the

evaluation. Cohen (1988) shows how to do

power calculations and you can also use the

statistical packages mentioned in Appendix B. 

8.5 Confidence intervals

Another way of showing the degree of

uncertainty in an estimate of the effect of an

intervention is through confidence intervals.

Suppose, that you do a study where people

taking a program improve their knowledge score

by an average of five points. It could be that the

program is actually useless but, just by chance,

this apparent benefit is found. Alternatively, the

program may really be worth more than a fivepoint improvement; but by chance you happen

to underestimate the real benefit. In other words,

the real benefit of the program might be higher or

lower than the observed value of five points. An

obvious question is: how much higher or lower?

You can often construct a confidence interval (as

illustrated in Appendix B), within which you are

reasonably sure the “true” level of benefit lies.

(The interval is calculated, taking into account

how much variability exists in individual

knowledge scores.) Typically, you see 95%

confidence intervals, which means that you are

95% sure (i.e., there is a probability of 95%) that

the size of the true effect is within the interval.37 

In many ways, the confidence interval is more

useful than a p-value, which simply indicates

whether a difference between groups is or is not

statistically significant. With a confidence

interval, you get a sense of just how high or low

the benefit might reasonably be.

The narrower the interval the better, since the

range of plausible values is smaller. Suppose, the

confidence interval shows that the observed

Chapter 8 Statistical issues

83

37 95% confidence intervals are based on = 0.05; 99% confidence intervals are based on = 0.01; etc.
value of the average benefit of the program (five

points) is from a one point benefit to a nine point

benefit. (Confidence intervals can be, but are not

always, symmetrical about the estimate of effect.)

Although your best estimate of the program

effect is still five points, it is also quite plausible

that the benefit could be as low as one point -

which we might consider trivial - or as high as

nine points, a very useful improvement. Thus,

we would be quite uncertain about the value of

the program. A smaller interval, of between four

and six points, would be preferable. All other

things being equal, a narrower interval can be

obtained with a larger sample size.

As a general rule, if a 95% confidence interval

excludes the value of zero, you will know that if

you tested the null hypothesis (i.e., no (zero)

difference between the values being compared),

you would be able to reject the hypothesis, using

alpha = 0.05.

8.6 Choosing the type of statistical

analysis

Up to this point we have simply referred to the

interpretation of the p-value and confidence

interval that result from a statistical analysis.

Before you get there, you need to think about

what type of statistical analysis to use. There are

a number of issues to consider. Some are

discussed in detail in this section; some later in

the chapter.

8.6.1 Type of data

The type of data being analyzed is important. If

you determine whether or not someone had any

injuries, you have what is called categorical or

discrete data; and if you use the actual number of

injuries occurring to each person or the counts

for an entire workplace you still have categorical

data. Continuous data can take essentially any

value in a range (at least in principle). Age is a

continuous variable, although in adults we

usually simply round off the number of years and

say that someone is 42, rather than 42.752 years

old. In practice, the boundary between

categorical and continuous variables can be a

little fuzzy. Thus a measure of behaviors, which

might take an integer value from 0 to 100, is

typically considered to be continuous. Some

statistical methods are robust which means that

taking such variables as continuous is acceptable.

Any variable that takes at least ten values can

reasonably be considered continuous. Another

situation in which the boundary between

categorical and continuous is fuzzy is when you

analyze injury rates. Although the rates are

continuous data, statistical tests intended for

categorical data are sometimes used. This is

because the analysis in such cases uses the actual

numbers of injuries, which are categorical

variables.

Statistical Issues Chapter 8

84

Things to consider when choosing the

type of statistical analysis

• What type of data is it - categorical or

continuous?

• What type of evaluation design is used?

• What is the unit of analysis?

• What is the study sample size?

• Is correction for different group

characteristics needed to avoid selection

effects?
8.6.2 Evaluation design

The choice of statistical analysis must also take

account of the evaluation design. A simple

comparison would be between the postintervention scores of those who have

experienced an intervention compared with those

who have not. Similarly, scores before and after

an intervention can be compared. The simplicity

of these two types of studies makes them useful

for distinguishing two situations which require

different analyses. In the first case, the scores in

the two groups all come from different

individuals. In the second case, in contrast, each

individual received two scores - before and after

the intervention. This is an example of a repeated

measures design. The two scores tend to be related,

since those who scoring higher before the

intervention will likely score high (or at least

relatively high) after the intervention. 

In analyzing repeated measures we can take

advantage of this relationship. The techniques

usually reduce the “noise” in the data, because

they remove much of the variability between

people. This allows the “signal”, the differences

over time within each person’s scores, to become

clearer.

Table 8.1 is a guide to statistical tests appropriate

for the designs that we have discussed. As

indicated, illustration of some of these tests can

be found in Appendix B.

Chapter 8 Statistical issues

85

Before-and-after Rate Chi-squared test for B.1.1

comparing rates

Continuous Paired t-test B.1.2

Pre-post with Rate z-test for comparing B.2.1

randomized or non- rate ratios or rate

randomized control differences

group 

Continuous Two sample t-test B.2.2

(groups similar) or 

multiple regression

(groups different)

Experimental designs Rate Chi-squared tests for B.3.1-B.3.2

with “after”-only comparing rates

measurements 

Continuous Two sample t-test B.3.3-B.3.4

(two similar groups),

ANOVA (two or

more similar groups),

or ANCOVA (two or

more different

groups)

Simple or multiple Categorical, rate or Time series analysis B.4 

time series; multiple continuous techniques

baseline design (e.g., ARIMA) 

across groups

Table 8.1: Choice of statistical test based on evaluation design and type of data

Type of design Type of outcome data Statistical test Section number
8.6.3 Unit of analysis

You also need to think about the unit of analysis.

If an intervention is targeted at changing a

workplace, rather than individuals, then each

workplace might count as just one unit. Another

possibility is that you conduct a randomized

study aimed at changing individual behavior, but

you randomize work groups, rather than

individuals. For example, if you have a company

with a number of small but geographically

separated units, you might randomize work

groups to receive or not receive the intervention.

Then in any given work group either everyone

gets the intervention or no one does. This

sampling of “clusters” rather than individuals

must be taken into account in the analysis. In

essence, the issue is that individuals may display

similar behavior within a given unit (i.e., a group

effect). The greater this tendency, the lower the

effective sample size. The concern about “cluster

sampling” is real and relatively common - but

often it is not accounted for in the analysis.

8.7 Avoiding pitfalls in data analysis

Data exploration

It is good practice before jumping into a

(relatively) sophisticated analysis to look at the

data in a fairly simple fashion. You can look at

the means of groups, the proportion of subjects

having injuries, frequency distributions or the

range of values observed. Graphs or diagrams

can often be helpful. These approaches give you

a “feel” for the data, as well as help find errors

arising from the data collection or processing.

Failure to do these things may lead to the

application of a technique inappropriate for the

data, or even worse, analyzing incorrect data.

Changes to the designs

It is often tempting, for practical purposes, to

“tweak” the intervention or evaluation designs,

to make what at face value might seem to be

minor changes. The result will generally have

important implications for the type of analyses

done. If you had originally planned the study

with a particular type of statistical approach, you

may not be able to use it. This is not to suggest

that you should always be rigid in following a

pre-planned design, but rather that you should

make changes with caution.

Other pitfalls

We have already mentioned a few pitfalls and

how to deal with them: choosing the right unit of

analysis - especially when we engage in “cluster”

sampling; ensuring studies are large enough to

have adequate power; and ensuring we do not

simply press buttons on our computer to produce

an answer based on an incorrect analysis. 

8.8 Summary

In this chapter, you have seen some basic

concepts in statistical inference, including pvalues, statistical power and confidence intervals.

We pointed out some of the things to consider

when undertaking an analysis: type of data;

evaluation design; unit of analysis; sample size;

and correction for group characteristics. Some

examples of analyses, corresponding to the

designs discussed in Chapters 3 and 4, can be

found in Appendix B.

Statistical Issues Chapter 8

86

Key points from Chapter 8

• Discuss the analysis with a friendly

statistician while designing the evaluation -

do not wait until after you have collected

the data.

• Check statistical power while designing the

evaluation.

• Do an initial data exploration to get a “feel”

for the data.

• Choose the type of statistical test according

to the type of evaluation design and the type

of data.

• If in doubt, discuss with a friendly

statistician.
87

Summary of recommended

practices

Chapter9

9.1 Introduction

9.2 Summary of recommended practices

We have discussed the various methods of

effectiveness evaluation in the context of

evaluating safety interventions. The following

section gives an overview of some of the key

messages from the previous chapters. You likely

will not be able to follow all of the recommended

practices. As a whole, they represent an ideal.

Even if you are not able to follow all of the

practices outlined in this guide, it does not mean

you should not proceed with your chosen

intervention and some level of its evaluation.

You will no doubt need to summarize and report

on the results of your evaluation. Some guidance

on this aspect has been included in Appendix C.

9.1 Introduction
Planning and development

• Identify resources available and information needs of the end-users of the evaluation results

• Involve all parties relevant to the intervention and evaluation in the planning stage, as well as at

subsequent stages of the evaluation

• Seek external expertise on evaluation design, methodology, and analysis, if necessary

• Review relevant theory, research literature, methodology, historical data

• Develop a conceptual model and/or program logic model

• Keep an intervention diary

Method development

• Determine reliability and validity of measurement methods if not already known; pilot test when

necessary

• Use qualitative methods to inform the use and design of quantitative methods

• Pilot test any qualitative or quantitative methods that are new

• Estimate statistical power based on planned methods - if insufficient choose new study sample

size, evaluation design or measurement method

Study sample

• Choose a study sample representative of the target population

• Use random sampling methods in selecting a sample from a sampling frame

• Choose a sample size large enough to give sufficient statistical power

• Consider using randomized block or matching designs to avoid selection effects

• In quasi-experimental designs (non-randomized), choose intervention and control groups so that

they are very similar

• In experimental designs, use randomization to assign participants to intervention and control groups

• In qualitative studies, choose a purposeful sampling strategy suitable for the evaluation purpose and

intervention circumstances

Recommended Practice Chapter 9

88

9.2 Summary of recommended practice
Evaluation design

• If you have no choice but to use a before-and-after design, for reasons of feasibility or ethics, try to

eliminate the threats to internal validity

• identify other changes in the workplace or community which could effect the outcome 

(history threat) and measure their effect

• ensure that before and after measurements are carried out using the same methodology, to

avoid instrumentation or reporting threats

• avoid using high-injury rate groups as the intervention group in a before-and-after study, to

avoid regression-to-the-mean threats

• allow for the fact that taking a test can have an effect of its own (testing threat)

• try to minimize Hawthorne threats by acclimatizing workplace parties to researchers before

measuring the intervention’s effect

• identify any natural changes in the population over time which could obscure the effect of the

intervention (maturation threat), and try to allow for them in the statistical analysis

• investigate whether the intervention participants’ dropping out could have and effect (dropout

threat)

• Use a quasi-experimental design whenever possible instead of a before-and-after design by using

one or more of the following strategies:

• include a control group

• take additional measurements both before and after the intervention

• stagger the introduction of the intervention to different groups

• add a reversal of the intervention

• use multiple outcome measures

• Use an experimental design whenever possible instead of a quasi-experimental design by assigning

participants to intervention and control groups through randomization

• When using control groups, check that intervention and control groups receive similar treatment

throughout the evaluation period, apart from the intervention itself; avoid, but check for, diffusion,

rivalry or resentment effects

• Plan a measurement timetable to capture maximum intervention effect and characterize longer

term effects

• Collect additional data to address threats to internal validity not addressed in the primary

experimental design

• Try to triangulate and complement data collection methods by using multiple methodologies,

especially qualitative and quantitative

Chapter 9 Recommended Practice

89
Measuring intervention implementation 

• Use both qualitative and quantitative methods to assess

• degree of intervention implementation

• problems with intervention implementation

Measuring intervention outcomes 

• Measure intermediate and final outcomes

• Use both quantitative and qualitative methods

• Select reliable and valid methods, appropriate for the study sample and intervention

• Consider injury statistics, other administrative records, behavioral/work-site observations, employee

surveys, analytical equipment and workplace audits as means of measuring outcomes.

• Select quantitative methods which give sufficient statistical power during analysis

• Consider the ethical aspects of measurement methods

Measuring unintended outcomes

• Use both qualitative and quantitative methods to assess any unintended outcomes

Statistical analysis

• Decide on the statistical methodology prior to undertaking evaluation

• Calculate power before data gathering begins – modify the design or measurement methods if

power is inadequate

• Use appropriate techniques for analysis based on type of data and experimental design

Interpretation

• Try to use the results of qualitative enquiry to enhance the understanding of the quantitative results

• Identify all likely alternative explanations for the observed results apart from the true effect of the

intervention (i.e., threats to internal validity)

• Examine the feasibility of alternative explanations, using a quantitative approach whenever possible

and collecting additional data if necessary

Conclusions

• Address evaluation questions in your conclusions

Recommended Practice Chapter 9

90
Glossary1

Alpha (): in statistical analysis, the probability you are willing to allow of concluding that the intervention

works, or does harm, when it is really ineffective

Before-and-after design: (syn. pre-post design) a research design where measurements are taken both

before and after the introduction of an intervention to measure its effect; permits less confident causal

inferences than a quasi-experimental or experimental design

Conceptual model: diagram which represents the causal relationships among important concepts relevant

to an intervention

Confidence interval: interval surrounding a point estimate, where the true value of the estimated

parameter is found with a probability of (1-)

Confounding variable: variable which affects both the independent variable (presence of intervention or

not) and the dependent variable of interest; it is not a mediating variable

Control group: group for which there is no intervention; group which is compared to the group

undergoing the intervention and the difference in group outcomes attributed to the effect of the

intervention; created through randomization in experimental designs; created using non-random means

in quasi-experimental designs

Effect modifying variable: variable which modifies the size and direction of the causal relationship

between two variables

Effectiveness evaluation: (syn. outcome evaluation; summative evaluation) evaluation which determines

whether a safety initiative had the effect (e.g., decrease injuries) it was intended to have

Evaluation design: the general plan for taking measurements during an evaluation; i.e., from how many

group(s) of workers/workers are measurements taken and when

Experimental design: a research design with both intervention and control groups created through a

randomization process

History threat (to internal validity): when some other influential event happens during the intervention

and evaluation period

Human sub-system (in the workplace): human knowledge, competencies, attitudes, perceptions,

motivations, behaviors

Implementation: putting the intervention in place

Glossary

91

1 This glossary is not intended to be used as a general reference for evaluation terms. In many cases, terms have been expressed in the same

context in which they are used in the guide. The definitions appearing here might therefore be more restrictive than they might be found in a more

general reference.
Instrumentation threat (to internal validity): when the measurement method changes during the

intervention and evaluation period

Inter-rater reliability: degree of agreement in scores between two different people rating the same

phenomenon

Intervening outcomes: outcomes which result from the intervention but precede the final outcome;

includes implementation, short-term outcomes, and intermediate outcomes

Intervention: see Safety intervention

Intervention group: group which undergoes the intervention; not a control group

Moderating variable: see effect modifying variable

P-value: in statistical analysis, the probability that a difference at least as large as the one seen could have

occurred simply by chance, if there really is no effect of the intervention

Power: see Statistical power

Program logic model: diagram depicting the linkage of intervention components to implementation

objectives to short-, intermediate- and long-term outcome objectives

Qualitative methods: research methodology which yields non-numerical data; includes interviews,

document analysis, observations

Quantitative methods: research methodology which yields numerical data

Quasi-experimental design: research design which permits more confident causal inference than a beforeand-after design; often includes a non-randomized control group

Random number tables: Tables consisting of randomly generated digits, 0 to 9, with each digit having a

probability 1:10 of being selected. Used to select random samples or to randomize participants to

intervention and control groups. 

Random sampling: technique of selecting a study sample so that the choice is made randomly (using

random number tables, etc.) and each participant has a known probability of being selected

Randomization: method of selecting participants for intervention and control groups such that the

probability of being selected into one or the other groups is the same for all participants; method of

forming intervention and control groups in experimental designs

Regression-to-the-mean threat (to internal validity): when a pre-intervention measurement of safety

for a group is atypical and later measurements over the course of the intervention and evaluation are more

similar to mean values

Reporting threat (to internal validity): when something changes the validity of (injury) reporting over

the course of the intervention and evaluation

Glossary

92
Reliability: degree to which the values measured for a certain concept are consistent

Safety intervention: any attempt to change how things are done in order to improve safety (e.g.,

engineering intervention, training program, administrative procedure)

Sample: see study sample

Sample size: the number of experimental units (people, workplaces, etc.) in the study sample

Sampling frame: the group within the target population from which you draw the study sample

Selection threat (to internal validity): when the apparent effect of the intervention could be due to

differences in the participants’ characteristics in the groups being compared

Selection interaction threats (to internal validity): when the apparent effect of the intervention could be

due to something happening to only one of the groups being compared in a experimental or quasiexperimental design

Statistical power: Likelihood of detecting a meaningful effect if an intervention is truly effective

Study sample: participants selected to undergo either intervention or control conditions in a research

design

Target population: larger group from which the study sample is selected; larger group to which evaluation

results should be generalizable

Technical sub-system (in the workplace): the organization, design and environment of work, including

hardware, software, job procedures, etc.

Testing threat (to internal validity): when the taking of the (pre-intervention) safety measurement for a

group has an effect on the subsequent measurements of safety for the group

Threats to internal validity: possible alternative explanations for observed evaluation results; typically,

experimental designs have less threats than quasi-experimental designs, which have less than a beforeand-after design

Unintended outcomes: outcomes of the intervention besides the intended ones; can be desirable or

undesirable

Validity: degree to which we measure the concept we intend to measure

Variable: any attribute, phenomenon or event that can have different quantitative values 

Glossary

93
Glossary

94
95

Some models to assist in

planning

AppendixA

Chapter 2 emphasized the importance of having

an explicit conceptual model and/or program

logic model related to the intervention. Since

there are three levels of interventions

(organization of safety management, technical

sub-system and human sub-system), we present

different models corresponding to each of these

three levels, and which can either be applied or

adapted for your own use. 

A.1 A model for interventions in the

technical sub-system

The first type of model is one most applicable to

interventions in the technical sub- system; i.e.,

interventions concerned with the organization,

design or environment of work, or with

secondary safety or emergency measures. Here,

the harm process is seen as a deviation, which, if

unchecked, develops into an exposure to

dangerous energies because of a loss of control

of the work process (see Figure A.1). Another

model of this nature is by Kjellén [1984].

As an illustration of how models can assist in

designing an evaluation, consider the application

of the first one to an engineering intervention

where one style of machine guarding is replaced

by a new one. Machine guarding is a specific

example of a “hazard control measure” depicted

in the model. (It would also be considered an

independent variable in the context of the

proposed intervention.) A typical evaluation

measures the frequency of damage processes or

injuries. (Injuries are a dependent variable and a

final outcome measure). By referring to the

model, one can identify intermediate variables to

measure (i.e., deviations from normal situation)

which here could be the percentage of times

during a given observation schedule the guard

A.1 A model for interventions in the technical sub-system

A.2 Models for interventions in the human sub-system

A.3 Models for interventions in the safety management

system
Appendix A

96

was not in place. The distinction in the model

between “damage process” and “reporting”

reminds us that injuries are not necessarily

reported, and so, any changes in other variables

affecting reporting should be accounted for

during the evaluation. 

In general, when dealing with interventions in

the technical-subsystem, one also needs to think

about the possibility of compensatory behavior

on the part of managers or workers and, if

necessary, account for this in the evaluation. For

example, interventions to reduce the levels of

noise emission from machines could be evaluated

by measuring the actual noise emissions.

However, there may be no effect of this

intervention on audiometric measures of hearing

loss if one result of quieter machines is that

workers use less hearing protection. Ideally, one

wants to include measures of noise emission,

protection equipment use and audiometric

measures in the evaluation.

2 Adapted from Hale and Glendon [1987]. Horizontal arrows from prevention or recovery activities indicate at which point they can curtail or stop

the harm development processes, which are represented by the vertical arrows running from the top to the bottom in the figure. If the

prevention/recovery activities are successful, movement down a vertical line shifts with a right angle to a horizontal prevention/recovery pathway;

if not, movement continues in a vertical direction.

Figure A.1: Deviation model 2
A.2 Models for interventions in the

human sub-system

When interventions are planned that do not

directly intervene in the work process, but are

designed to modify human knowledge,

competence, attitudes or behavior, it is valuable

to use a specific model to help guide the research.

Even when an intervention in the technical subsystem is planned, behavioral models could be

relevant for the steps in the deviation which

involve human activity. We present two

behavioral models. One is concerned with errors

made without the intention to take risk; the other

is concerned with intentional risk taking.

Model relevant to unintentional risk-taking 

Figure A.23 shows a model of three types of error

mechanisms that can occur without the intention

of taking risk. “Slips” (of action) and “lapses”

(of memory) can happen in the absence of a

problem in the environment and result in the

failure to execute a plan as intended. When

operators realize that a problem exists, theory

suggests that people will most likely search for

familiar patterns and try to apply a known

problem-handling rule. Only if the “rule-based

level” approach fails, do people then resort to a

“knowledge-based level” approach. This

involves a wider range of cognitive strategies. In

this model, errors arising at the rule-based and

knowledge-based levels are called “mistakes”.

They result from carrying out an inadequate plan

in the face of a problem. A model from Hale and

Glendon [1987] develops the problem-solving

aspects of Reason’s model into a number of

specific steps which can also be useful for

evaluation planning. Both models indicate which

intervening variables are possibly relevant to

interventions aimed at modifying normal

working behavior.

Model relevant to intentional risk-taking

The other type of model relevant to the human

sub-system is one concerned with intentional

risk-taking. The Health Belief Model4 (Figure

A.3) has been frequently used in the health

promotion field in relation to health-related

behaviors, such as smoking. However, the

underlying theory is likely relevant to decisions

and behaviors in safety and occupational health

contexts. It can be applied to observing safety

rules, using personal protective equipment and

dismantling safety guards, etc. by workers; and,

with modification, to observing safety rules and

regulations by managers designing, planning and

monitoring work processes. 

The model shows that the likelihood of

undertaking the recommended health (or safety)

action depends on the individual’s perceptions

of their susceptibility to disease/injury, its

seriousness, the benefits of taking the preventive

action and the barriers to taking such action.

Benefits are things like saving time and effort,

and approval from a production-oriented

supervisor, etc. Barriers are things like

inconvenience, lack of knowledge or skill in

undertaking the new behavior, fear of countering

local norms, etc. All of these categories provide

ideas about the intervening attitude measures

that can be taken in evaluations of behavioral

interventions.

Appendix A

97

3 Figure from Reason [1990] is reprinted with the permission of Cambridge University Press.

4 Becker MH, Haefner KP, Kasl SV, Kirscht JP, Maiman LA, Rosenstock IM [1977]. Selected psychosocial models and correlates of individual healthrelated behaviors. Med Care 15:27-46. With permission of Lippincott Williams & Wilkins.
Appendix A

98

Figure A.2: Generic error-modeling system [Reason 1990]
A.3 Models for interventions in the

safety management system

When we move to interventions at the level of

the organization (i.e., interventions to change

workplace safety policies, procedures, structures,

organization), the causal chain between the

intervention and the final outcome measures of,

for example, injury, becomes even longer. It is

therefore much more difficult to find evidence

for this link in a convincing way. Thus, there is

an even greater need to measure intermediate

outcomes as well. Few comprehensive

organizational models exist, linking aspects of

management structure all the way through to the

injury process. The model in Figure A.4 is one

which attempts to do this.

The model shows a management system as an

interacting set of tasks, controls and resources,

linked by communications and feedback loops,

that develops, operates, monitors and improves

a risk control and monitoring system (RCMS).

The RCMS carries out risk analysis and plans all

of the control functions and activities, including

the system for monitoring the performance of the

risk control system. The outputs to the technical

and human sub-systems in the management

model can be seen as the links to the earlier

models (Sections A.1 and A.2). The management

policy-making system sets up the RCMS,

alongside the other aspect systems of the

company (such as quality, environment or

productivity), reviews it and gives it signals to

improve. These loops make it a dynamic,

learning system.

Appendix A

99

Figure A.3: Health belief model 5

5 Becker MH, Haefner KP, Kasl SV, Kirscht JP, Maiman LA, Rosenstock IM [1977]. Selected psychosocial models and correlates of individual healthrelated behaviors. Med Care 15:27-46. With permission of Lippincott Williams & Wilkins.
Appendix A

100

Figure A.4: Model of a safety management system6

6 Model from Hale et al. [1999]
Appendix A

101

The eight delivery systems, referred to in the

figure, deliver for each primary business function

the following generic controls and resources to

the requisite safety-critical tasks:

• people available when required to perform

safety-critical tasks

• competent in performing them and

• committed to safety; 

• clear output goals, procedures, rules and plans

for safety; 

• hardware resources of well designed work

interfaces, tools and equipment that can be

worked safely; 

• spares, replacements and modifications to plant

and equipment that maintain safety;

• communication and coordination channels for

ensuring that information about safety is

disseminated to the right people, and that

tasks performed by different people are safely

coordinated; 

• mechanisms for resolving conflicts among safety

and other criteria.

Each delivery system actually involves a number

of steps or sub-tasks. For example, the first

delivery system mentioned - delivering people -

involves analysing their tasks; specifying the

personnel requirements; selecting and training

the right people; and allocating them to the work

at the appropriate times to perform their safetycritical functions.

Interventions at the level of the management

system can be done to introduce or improve the

functioning of any one of the elements of the

model, or a combination of them. Examples

include involving operators in writing safety

procedures; adopting a new safety audit system

to review the RCMS; appointing a review

committee to check proposed plant modifications

for safety and health implications; and

introducing ergonomic standards for purchasing

tools and equipment. This model therefore

provides possible sets of intervening variables to

link the management interventions to the

ultimate change in injury experience in the

deviation model. 
Appendix A

102
103

Examples of statistical analyses

AppendixB

B.1 Analyses for before-and-after designs

B.1.1 Before-and-after design with injury rate data

B.1.2 Before-and-after design with continuous data

B.2 Analyses with pre-post measures and a control group

B.2.1 Pre-post with control group and rate data

B.2.2 Pre-post with control group and continuous data

B.3 Analyses for designs with after-only measures and a

control group

B.3.1 After-only measurements with two groups and rate data

B.3.2 After-only measurements with several groups and rate data

B.3.3 After-only measurements with two groups and continuous data

B.3.4 After-only measurements with several groups and continuous 

data

B.4 Multiple measurements over time
This appendix shows some simple statistical

analyses. We assume that you have a computer

with a statistical software package, or if not, can

get a book that explains statistical calculations.

Some well-liked basic texts are Altman [1991];

Armitage and Berry [1994]; Clarke [1980]; Colton

[1974]; Freedman et al. [1998]; Healey [1984];

Norman and Streiner [1994]; Siegel and Castellan

[1988]; Swinscow [1978]; Weinberg and Goldberg

[1990]. Some of the techniques you might need

are available in spreadsheet software packages -

but they have their limitations. We demonstrate

how to do some analyses not typically found in

most packages.

Reasonably good statistical applications are fairly

cheap (many universities have site licences) and

some can be downloaded free from the Internet.

Two products, available at the time of writing,

include: the widely used Epi Info, a DOS-based

word processing (questionnaire design), database

and statistical program

(http://www.cdc.gov/epo/epi/epiinfo.html);

and PEPI (http://www.usd-inc.com/pepi.html),

a statistical package with many useful statistical

procedures. 

Keep in mind that most statistical tests make

certain assumptions about the real world, which

may or may not be true in your situation. We

mention a few of these when they are particularly

relevant. 

The examples included in this chapter are

organized according to the evaluation designs

presented in Chapters 3 and 4. For some, we

show how to do the calculations. For others we

show examples from published papers. In some

of these cases (e.g. paired t-test, two-sample ttest), any statistical package will do the

computations.

B.1 Analyses for before-and-after

designs

B.1.1 Before-and-after design with injury rate

data7

Calculating a p-value

Much injury data is in the form of rates. Typically

they are expressed in the form:

The denominator could also be the number of

people working in a plant in a given year. You

may want to compare two rates in one

workplace, before and after an intervention. The

hypothesis here is that the intervention has no

effect, i.e., no difference between the two

measurements, apart from chance variability.

The data are in Table B.4. (Note that it is

important to do the calculations as accurately as

possible, so do not round off numbers on your

calculator until the very end of the analysis. For

ease of reading we round off below, but we have

already done the calculations more precisely.)

Are the rates 70 (per 100,000 hours worked) and

37 significantly different? The approach is to see

how many injuries are expected to occur if the

total rate, in both time periods combined, is

applied to the Before and After groups - as if there

is no true difference between groups. You then

compare the observed (actual) numbers of

injuries with those expected. In this case, the

overall rate is 50 (per 100,000 hours). So the

expected number of injuries in the Before group

is (50/100,000) x 40,000 = 20, and in the After

group is (50/100,000) x 60,000 = 30.

Appendix B

104

7 The method described here assumes that the risks of an injury before-and-after are “independent.” Strictly speaking, with many of the same

people working that may not be true, but we are reasonably safe in using this approach. If most injuries were occurring to the same few people

before and after the intervention, we would need to use a more sophisticated statistical technique.
Now you calculate the test statistic (X2

):

where ∑ (the Greek letter sigma) means you add

up the quantities (Observed - Expected)2 /

Expected for all the groups. For the data here, 

X2 = [(28 - 20)2 / 20] + [(22 - 30)2 / 30] = 5.33.

You compare the calculated value of 5.33 with

critical values of something called the chi- squared

(2 ) distribution with one degree of freedom8

. For

5% significance (i.e.,  = 0.05), 2 = 3.84, and the

calculated value 5.33 is larger than this. This

means that our result is statistically significant,

i.e., the probability of getting a difference in rates

as large or larger than was found is less than 5%,

if there really is no effect of the intervention. (A

computer program gives the precise p-value: p =

0.021.)

Calculating rate ratios and rate differences

One limitation of this method is that it does not

indicate the strength of the effect of the

intervention. How can you measure that? We

describe two obvious ways. The first is to look at

the relative injury rate. Take the rate after the

intervention and divide by the rate before. Call

the result RR (for Rate Ratio), which in this case

is 36.7 / 70 = 0.52, or 52%. You could also say

that the rate has dropped by 100 - 52 = 48%. The

second measure is simply the difference in the

rates, RD. Here RD is 70 - 36.7 = 33.3 per 100,000

hours worked.

Calculating a confidence interval for a rate

ratio

You can calculate a confidence interval (CI) for

these estimates. As described in Section 8.5, a

confidence interval is a range of values within

which the true value of the parameter lies, with

a probability of (100 - )%, usually 95%. Let us

start with the RR. For reasons we will not go into,

the analysis uses natural logarithms, abbreviated

as “ln” on your calculator. The CI for ln(RR) is

given by the limits:

ln(RR)  Z x SE,

where  means plus or minus. Z is a number

you can look up in a statistical table of critical

values from the normal distribution. Its value

depends on whether you want a 95% CI or 90%

or some other value. [We use the conventional

95%, for which the appropriate value of Z is 1.96.]

Appendix B

105

Before Intervention After Intervention Total 

Number of injuries 28 22 50 

Employee hours 40000 60000 100000

Number of

injuries/105 hours 70 37 50 

Table B.4: Injury rate data from a before-and-after evaluation design

Note of caution: This method works well

when the numbers of injuries are not too

small. A reasonable rule here is that the

number of injuries in each group should be

at least five. If it is less, you can use a different

statistical approach known as an exact

method, which would likely require a

computer. 

8 Degrees of freedom are used a lot in statistics. We will not go into any detail, but simply point out that in this situation the number of degrees

of freedom is one less than the number of groups.
SE is something called the Standard Error and in

this case it refers to the Standard Error of ln(RR). 

The Rate Ratio = 36.7 / 70 = 0.52, and a calculator

shows ln(0.52) = -0.65. You now need to calculate

the Standard Error (SE). It is not too complicated.

Take the reciprocal (1 divided by the number) of

the number of injuries in each time period, add

the reciprocals up, and take the square root of the

sum. The reciprocals are 1/28 and 1/22. Adding

them gives 0.08, and the square root of that is

0.28. With our data, the 95% CI for ln(RR) is then:

-0.65  (1.96 x 0.28) = -1.2 to -0.09.

Since this is the CI for ln(RR), you now need to

take antilogs to get the CI for the Rate Ratio (RR)

itself. (On your calculator, you get antilogs with

the button that reads “ex ”). This gives the CI for

RR as 0.30 to 0.92. In other words, you are 95%

sure that the true value for the Rate Ratio is

between 0.30 and 0.92.

Calculating a confidence interval for a rate

difference

Now let us work out the CI for the RD, the

difference in rates. The CI for RD is given by the

limits:

RD  (Z x SE).

You earlier calculated rates per 100,000 hours (not

per hour) to avoid lots of zeros after the decimal

point. This means you can use time units of

100,000 hours, which makes things a little easier

on your calculator. You found earlier that the RD

is 33.3 per 100,000 hours. You again need to get

the SE - the Standard Error of RD in this case.

This time you calculate # injuries / (# time units)2

for each of the time periods, add them up and

take the square root of the sum. 

Thus, 

For the 95% CI, 

RD  (1.96 x SE) = 33.33  (1.96 x 15.37) 

= 3.22 to 63.45.

The CIs for RR and RD show that you cannot rule

out that the effect could be quite small or very

large. Your best estimate of each, though, is still

the value you actually found from the data, e.g.,

33.3 is the best estimate of RD.

What is the appropriate “before”

measurement when you have historical data?

In our example above, we have a situation where

the periods of time before and after the

introduction of the intervention are similar in

length. What do you do in a situation where, for

example, you have injury rate data for several

years before the intervention, as well as for one

year after the intervention’s introduction? Some

people would propose calculating the “before”

measure from the data of several years. This is

generally not recommended, since many things

can change over such a long period of time. 

On the other hand, the historical data are useful

for judging whether or not the most recent rate

measurement for the period just before the

intervention - your candidate “before”

measurement - is typical of the preceding years.

If it is atypical, then consider regression-to-themean as a possible threat to internal validity. If

there is any suggestion from the historical data

that a trend over time is occurring, you would be

well-advised to use the time series methods

described in Section B.4 for your analysis instead

of the above test.

B.1.2 Before-and-after design with

continuous data

The next illustration is also concerned with

before-and-after designs, but in this case the data

are continuous. We will refer to a paper by

Robins et al. [1990] which used several statistical

methods. The study was of a large U.S.

Appendix B

106

SUM = [28 / 0.42] + [22 / 0.62] = 236.11

SE = SUM = 236.11 = 15.37
manufacturing firm with 50 plants. The

intervention was designed to bring the company

into compliance with the U.S. Federal Hazards

Communications Standard (HCS), informing

workers about work-related hazardous

substances, the potential consequences of

exposure, detection and protection. The ultimate

goal of the HCS is to reduce chemically related

occupational illnesses and injuries. 

Trainers were trained, and worked with union

and management, who jointly developed and

implemented the programs at each plant. The

evaluation was designed to assess the planning

and implementation, attitudes and knowledge,

work practices, working conditions and

organizational impacts. (The authors did

examine changes in rates of illness and injury, but

because of a change in the classification system,

decided they could draw no conclusions.) Five

plants, representing the variety of manufacturing

processes, were chosen as sites for data collection.

At each plant, data were collected in three phases

- phase one, as the training was being completed;

phase two, one year later; and phase three, a

further year later, i.e., two years after the training.

Although the design had three measurement

times, the data were analysed by comparisons of

the measures at two times - e.g., phase one with

phase two. Information was collected from

various sources, including semi-structured

interviews, feedback sessions, observations and

questionnaires. The questionnaires were given

to about 50 hourly paid employees at each of the

five plants. One hundred and twenty-five

employees answered questions on work practices

at both phases one and two. A composite score

was calculated as the average response to the

questions, which were rated from 1 = never to 4

= always. The hypothesis being tested involved

whether the program was effective in changing

work practices from phase one to phase two.

Statistically, you start with a null hypothesis that

the difference in practices between the phases

should be zero. The observed mean score for this

group was 2.80 at phase one and 2.92 at phase

two. 

Thus, the observed difference between phases

was not zero but rather 0.12. The next step was to

see if this difference was statistically significant or

not. Since each person’s composite score was the

average of responses to several questions, it was

reasonable to consider the data as continuous.

As well, since the data were paired - each

individual provided a pair of scores, with one at

each phase - the appropriate statistical test was

the paired t-test. This method produces a tstatistic, which can be looked up in a table to

determine the p-value - computer printouts give

this automatically. The authors reported the pvalue to be 0.07. Using a cut point (significance

level) of 0.05, the result was thus not statistically

significant. Therefore, the null hypothesis could

not be rejected. 

B.2 Analyses with pre-post measures

and a control group

B.2.1 Pre-post with control group and rate

data

The wrong way to compare pre-post rate

changes in two groups

As noted in earlier chapters, you should always

use a control group - randomized or nonrandomized - if at all possible, since rates before

and after an intervention can differ for reasons

that have nothing to do with the intervention.

Suppose you collect the data in Table B.5. You

might think you could do a before-after

comparison for each group, using the method

shown in Section B.1.1, and see if there was a

significant drop in the rate in the intervention

group, but a non-significant one in the controls. 

The problem is, it is WRONG! To see why, look

at Table B.5. In the intervention group, the

“before” rate is 7.3 injuries per 100 FTE workers.

The “after” rate is 4.1. Calculations, as shown in

section B.1.1, might find p = 0.048, i.e., just

statistically significant. In the controls, the

“before” rate is 7.7, and the “after” rate is 4.6,

giving p = 0.052, not quite significant. This could

lead you to think that the intervention is effective.

Appendix B

107
In fact, the appropriate statistical test compares

the before-after difference in the intervention

group (3.2) with the difference in the controls

(3.1). (You are examining a difference of

differences!) If you do the calculations (we show

you how in another example below), you would

find that it is NOT significant, showing you

cannot claim the intervention works - something

else likely led to the drop in rates in both groups.

Now there is another way to think of these data.

You could look at the relative (or proportional)

values of the rates as we did in section B.1.1. The

rate ratios are 56% in the intervention group and

60% in the controls. (You could also say that there

was a 44% drop in rate in the intervention group

and 40% in the controls.) Some statisticians view

this as a better way to consider the data. One

reason for this is that if the groups have quite

different initial rates, then one of the groups can

improve a lot more than the other based on the

difference in rates. For example, if Group One

has a Before rate of 4.3 and an After rate of 1.2, a

difference of 3.1, then if Group Two’s Before rate

is 2.9, its rate cannot possibly be reduced as much

as Group One’s, even if it has no injuries at all!

This problem does not apply to relative changes,

which cannot exceed 100%. 

Comparing the pre-post rate changes in two

groups using rate ratios

We now show you the two methods for

comparing the change in an intervention group

versus the change in a control group. The

statistical methods for analyzing rate differences

and rate ratios are not the same. First, let us look

at rate ratios. We will use the data in Table B.6

and show you how to calculate the test statistic,

z, using rate ratios

We start by going through some calculations

similar to those in Section B.1.1. Get the ln(RR)

for each group. (We use subscripts 1 and 2 to

represent the two groups.)

ln(RR1) = ln(5.74/6.00) = -0.043,

ln(RR2) = ln(2.03/6.40) = -1.149.

Then calculate the difference between these, D: 

D = ln(RR1) - ln(RR2) = -0.043 -(-1.149) = 1.106.

You need the Standard Error (SE) of this

difference as well. Simply take the reciprocal of

the number of injuries in each of the four

pre/post, control/intervention categories, add

them up and take the square root of the sum. The

reciprocals are 1/49, 1/46, 1/26, and 1/8.

Adding them gives 0.206, and the square root of

that is 0.453.

Now calculate the test statistic, z:

z = D / SE = 1.106 / 0.453 = 2.44. 

When z is bigger than 1.96 - the critical value

from the normal distribution, when  = 0.05 - as

it is here, the difference in (the ln of) the rate ratios

is statistically significant. Thus, the data suggest

the intervention works. 

Appendix B

108

Period of Injury Rate Intervention Group Control Group

Measurement 

Pre-intervention 7.3 7.7

Post-intervention 4.1 4.6

Table B.5: Injury rate data from a pre-post with control group evaluation design

(injuries per 100 FTE workers)
Comparing the pre-post rate changes in two

groups using rate differences

Let’s do the calculations based on the difference

in rates, rather than the ratio. You used rates per

100,000 hours so you can use time units of 100,000

hours for the rate differences.

RD1 = 6.00 - 5.74 = 0.26,

RD2 = 6.40 - 2.03 = 4.37.

And the difference between them is calculated

by subtracting the RD for the control group from

the RD for the intervention group.

D = RD2 - RD1 = 4.37 - 0.26 = 4.11.

Again you need the SE of the difference. In this

case, calculate # injuries/(#time units)2 for each of

the four categories, add them up and take the

square root of the sum:

As before, calculate the test statistic, z:

z = D / SE = 4.11/ 1.88 = 2.19. 

This z is bigger than 1.96, so this analysis also

provides evidence that the intervention works.

Notice that the z values calculated by the rate

ratio and rate difference methods are not quite

the same. This is because the analyses have

actually tested different hypotheses. If the preintervention values are different, then it is

possible for the hypothesis about rate ratios to be

true, but that for rate differences to be false; or

for the rate difference hypothesis to be true, but

the rate ratio one to be false. For example, the

pre and post rates for controls could be 12 and 9

respectively; those for the intervention group

might be 6 and 3. The rate difference is the same,

but the ratios are quite different - 75% and 50%.

Likewise, suppose the control group’s rates pre

and post were 12 and 6, respectively, compared

with 6 and 3 for the intervention group. The rate

ratios are the same, but the rate differences are

not - they are 6 and 3. 

In practice, if the pre-intervention rates are very

different, you should be concerned about a

potential selection threat to internal validity.

When you have chosen the controls well, the preintervention rates in the two groups should be

similar, in which case the two analyses should

give reasonably similar conclusions. If you are

concerned about moderate differences between

the groups, consult a statistician - there are ways

to make adjustments to your analysis through

multiple regression analyses.

Appendix B

109

Pre-intervention Post-intervention 

Control Injuries 49 46

(Group 1) Hours 817000 801000 

Rate per 100,000 hrs. 6 5.74

Intervention Injuries 26 8

(Group 2) Hours 406000 394000 

Rate per 100,000 hrs. 6.4 2.03 

Table B.6: Injury rate data from a pre-post with control group evaluation design

SUM = 49/8.172 + 46/8.012 + 26/4.062

+ 8/3.942 = 3.54

SE = SUM = 3.54 = 1.88.
B.2.2 Pre-post with control group and

continuous data

Section B.1.2 demonstrated how to compare

before and after scores on a continuous scale for

a single group. Essentially, you take the

difference score (pre - post) for each person and

work with those values in the analysis. With two

groups (intervention and control), you can do the

same thing. Then for each group you have the

difference scores for all the people in the group

and you have reduced the data to a single

difference score for each person. If the

intervention is ineffective, then there should be

no difference in the means of these difference

scores between the groups. The way to see if any

difference is statistically significant or not is to

do another type of t-test. You have two groups;

so this is called the two-sample t-test. It is in any

computer package or textbook.

What do you do when there are differences in the

characteristics of participants in the intervention

and control groups that might influence how they

respond to an intervention? In such a situation,

apply a more sophisticated technique that allows

a correction of these differences, such as some

form of multiple regression.

B.3 Analyses for designs with afteronly measures and a control

group

When you only obtain measurements after the

intervention and not beforehand, you can have a

problem if the subjects are not randomized to

intervention or control group. This is because

the groups may have been quite different at the

start. For this reason, in chapter 4, we

recommended “after”-only designs only when

using groups formed through randomization.

We therefore expect the statistical methods of this

section to be used primarily in such situations.

However they can sometimes be used - with

caution - in the absence of randomization,

especially if there is information on potential

confounders post-intervention. If so, statistical

techniques are available that can use this extra

data. As you can imagine, they are too

complicated for this appendix - you will have to

talk to a statistician - but we mention some of

them here.

B.3.1 After-only measurements with two

groups and rate data

The same statistical test, 2, is used as in the

before-and-after design with rate data (Section

B.1.1), but because you have two different groups

of workers, the cautionary footnote no longer

applies.

B.3.2 After-only measurements with several

groups and rate data

Sometimes you might have several groups, for

example one control and others in which different

interventions are carried out (Table B.7). This

time our hypothesis is that none of the

interventions work; so we expect the rates in all

the groups to be the same. Notice that if even

one of the interventions works, our hypothesis is

contradicted. A simple approach might be to

compare each intervention group with the control

group, using the test indicated in the preceding

section (B.3.1). However, this would be invalid

because it involves multiple testing.9 Instead, we

use an approach similar to the one for two

groups.

Again, use the overall rate to estimate the

expected number of injuries in each group,

assuming the overall rate applies to all groups.

For example, for the control group, the expected

number of injuries = (150 / 250,000) x 60,000 =

36.0. The equivalent values for the other three

groups are 42.0, 30.0, and 42.0. 

Appendix B

110

9 Multiple testing means you are doing more than one test at the same time. If you do each one using an alpha of 0.05, the probability that at

least one of the tests is significant is more than 0.05, sometimes considerably more. You have to make an adjustment or use a different method,

as is done here, to keep the overall alpha at 0.05.
Again, calculate X2:

This time there are 4 quantities to add up, each

corresponding to one of the four groups:

X2 = [(43-36)2

/36] + [(47-42)2/42] +

[(36-30)2

/30] + [(24-42)2/42] = 10.87.

Again, compare this with the chi-squared

distribution. The number of degrees of freedom

is one less than the number of group measures

being compared, i.e., , 4 - 1 = 3. A chi-squared

table shows the 5% significance point is 7.81. Our

X2 is bigger than this, so again, it is statistically

significant, i.e., , p < 0.05. (The actual p-value is

0.012). Note that this method does not work

properly if the number of injuries is small (less

than 5) in one or more of the groups. In such

cases, you need to use an exact method.

B.3.3 After-only measurements with two

groups and continuous data

If there are two groups with after-only measures,

you have the same situation as described in

Section B.2.2, with a series of scores for each of the

two groups. You may want to see if any

difference is statistically significant. Again do a

two-sample t-test.

B.3.4 After-only measurements with several

groups and continuous data

Survey questions in the Robins et al. study

described earlier also asked about the extent to

which workers followed certain work practices.

The responses for each item ranged from 1 =

“never”/”almost never” to 4 = “always”, and an

average was calculated to give a scale score. For

each plant, the mean scores of individuals were

calculated. These means ranged from 2.42 to 3.06. 

The hypothesis tested was that there was no

difference in work practices between plants.

Once again, the data were treated as continuous,

but this time with the means of several groups

compared. Whereas the two-sample t-test

applied to a comparison of the means of two

groups, the generalization of this to several

groups is called a one-way Analysis of Variance

(ANOVA). ANOVA is actually a generic name

for a range of procedures, of which this is a

particular example. The method produces an Fstatistic, and a subsequent p-value. In this case,

p = 0.004. Thus, the result is statistically

significant, and we conclude that the differences

in observed means are not due simply to chance. 

As with the 2 x 5 table discussed earlier, the

method does not tell us which means are

different from others. In fact, with five groups,

Appendix B

111

Table B.7: Example injury data from an experimental design with post-only measurements and

multiple intervention groups

Control Intervention Intervention Intervention Calculated

1 2 3 Total 

Injuries 43 47 36 24 150 

Hrs. 60000 70000 50000 70000 250000 

Rate/105 hrs. 71.7 67.1 72 34.3 60 

Expected 36 42 30 42 

number of

injuries
there are ten possible comparisons between pairs

of groups. This raises the issue of multiple

testing, described earlier. You should only

consider testing individual pairs if the “overall”

F-test is significant. Various text books

demonstrate how these pairwise comparisons,

allowing for multiple testing, are made10.

In a quasi-experimental (and sometimes in a truly

experimental) setting, it is important to remove

the effects of any characteristics of individuals

that may affect the outcome measure. For

example, older workers may behave more safely

on the job. If this is true, and the intervention

group contains more older workers, it will likely

have better outcomes following the intervention

than the comparison group, regardless of the

value of the intervention. Likewise, if the

comparison group is older, we may fail to see a

real effect of the intervention. Statistically, you

can allow for the age effect, to obtain a more

proper estimate of the impact of the intervention.

(The technical term for these adjustment variables

is confounders.) 

Robins et al, in the example above, noted known

differences in the people surveyed in each plant.

Several variables were listed where the

respondents differed in occupation, degree of job

hazard, age, education level, and number of years

in the plant. There was obvious concern that if

work practices varied by age and more older

people worked at some plants, then this disparity

(and others like it) - rather than the training

program - could have accounted for the

significant differences. This would threaten

internal validity through a selection bias. A

statistical approach that combines ANOVA with

allowance for these confounders (covariates) is

needed. The answer is a technique called

analysis of covariance (often abbreviated as

ANCOVA). The authors reported that in their

study the new analysis did not change the basic

conclusions about differences in work practices. 

B.4 Multiple measurements over time

Komaki et al. [1980] reported the effect of an

intervention involving training and feedback.

Concerned that training alone was not sufficient

to produce behavioral change, a “multiple

baseline design across groups” was applied with

four sections of a city’s vehicle maintenance

division. (This design was described in section

4.2.3.) Five “conditions”, each lasting for several

weeks, were used: 1) Baseline; 2) Training only I;

3) Training and Feedback I; 4) Training only II; 5)

Training and Feedback II. (i.e., after a Baseline

period, there was a period when only training

was given (Training only I), followed by one that

also included feedback (Training and Feedback

I). Feedback was then dropped (Training only

II), before being reinstated (Training and

Feedback II). Since the study was done in four

sections of the workplace, the times for the

changeover from one condition to another

differed. (This allowed the authors to check on

whether or not other changes at the work-site

unrelated to the intervention might have

influenced behavior.) 

The main outcome measure was of the safe

performance of tasks, measured by behavioral

observations. Observations were made several

times a week and plotted to give a weekly

average of the percentage of incidents performed

safely in each maintenance section. Since the

conditions each lasted from five to eleven weeks,

there were multiple measures before and during

each condition, with approximately 45

observations for each section over the course of

the evaluation. Such data are a form of repeated

measures known as time series data. 

The authors wanted to allow for general trends in

safe behavior, as well as see if the change from

one condition to the next led to a switch in

behavior. The appropriate method for this form

of time series is known as ARIMA - auto

regressive integrated moving averages. Now the

Appendix B

112

10 For example Kleinbaum et al. [1988]
name might seem enough to put you off statistics

for life. What is important is that it takes account

of correlations from measurement to

measurement (auto correlation) - if the

percentage was high in one week, it was likely

to have been relatively high the next week. The

data are too complex to describe in detail here.

Nevertheless, the general message from the

evaluation was clear. Without feedback as well,

training showed relatively little effect.

Time series analyses are appropriate in a situation

where there are repeated measurements on the

same subjects, e.g., when taking behavioral

measurements. They are also appropriate when

there are trends in workplace data due to changes

in the business cycle, weather etc. 

There are occasions, perhaps after an intervention

is in place and running well, when the injury rate

is expected to remain stable over time. Yet

because a single plant may experience only a few

injuries per month, the monthly rate may vary

considerably simply because of random

variability. To check if the results for a single

month are significantly out-of-line with previous

experience, you can use control charts. They are

used in quality control settings, perhaps to make

sure that the size of ball bearings is within a small

range. They can be readily adapted to workplace

safety.

As an example, suppose that on average there

are three injuries per month. (We assume the

number of hours worked is constant; if not, you

can use the average rate with its standard

deviation, a measure of month-to-month

variability in the rate.) Sometimes, there will be

only one or two injuries in a month, or maybe 4

or 5. In fact, the probability of only one in any

month is about 10%, while the probability of five

is about 10%. Even 6 in a month will happen

about 5% of the time, so might well occur at some

point in a two-year period. This means you

shouldn’t be too quick to push the panic button

when one month’s figures are somewhat higher

than normal. But by the same token, you

shouldn’t be smug if in one month there are no

injuries at all. 

Control chart methodology will alert you when

the number of injuries in a month is so high that

there seems to be a real problem, or when the

pattern over two or three months is a cause for

concern.

Appendix B

113
Appendix B

114
115

Reporting your evaluation results

AppendixC

C.1 Introduction

C.2 Evaluation report

C.2.1 Structure of the report

C.2.2 Clear language

C.2.3 Audience specificity

C.3 Communicating beyond the report

C.4 Summary

C.1 Introduction

Most of this guide has focused on the

methodology required to do a good intervention

effectiveness evaluation. This appendix focuses

on what to do with the results of the evaluation.

Written reports are the usual way to summarize

them, even when an evaluation is done in-house.

Not only does this provide a record for the

organization, the process of writing the report

also encourages a critical examination and

synthesis of the evaluation activities and results.

We will describe the sections that people typically

include in a report. We will also discuss how

your communication strategy should extend

beyond the report itself.

C.2 Evaluation report

C.2.1 Structure of the report

Table C.1 lists what you would typically include

in a report. First is the abstract/executive

summary, which incorporates the main points of

the introduction, methods, results, discussion and

conclusion sections. This is typically one or two

pages in length. This summary is an important

since, for many readers, this might be the only

section they read in its entirety.

• The introduction presents the goals of the

intervention, the intervention itself and the

general approach taken in the evaluation. 

• Methods/procedures then describe the

evaluation methods in detail. 

• Results present the data gathered through the

evaluation which address the evaluation
questions. This section should present the

results not only in text, but also through

figures, graphs and tables. These visual

summaries facilitate uptake of the information

for many readers. 

• Many reports include a discussion section,

which should lead the reader from the results

to the conclusion. Whereas the results section

gives a logical presentation of the results, the

discussion synthesizes and interprets them

with reference to current theory and

understanding. The discussion section is also

the place to consider threats to the internal

validity of the evaluation, including any

reasoning based on theory or data from

outside of the evaluation. 

• The conclusions summarize what is

concluded from the data and, possibly, any

resulting recommendations. Conclusions

should address the main evaluation questions. 

• In fact, as much as possible, the entire report

should be constructed so that the relationship

of the various methods and results subsections to the evaluation questions and

conclusions is clear.

Appendix C

116

Abstract/executive • Overview of the program and evaluation

summary • General results, conclusions and recommendations 

Introduction • Purpose of the evaluation

• Program and participant description (including staff, materials, 

activities, procedures, etc.)

• Goals and objectives

• Evaluation questions 

Methods/procedures • Design of the evaluation

• Target population

• Instruments (e.g., questionnaire)

• Sampling procedures

• Data collection procedures

• Validity and reliability

• Limitations

• Data analyses procedures 

Results • Description of findings from data analyses

• Answers to evaluation questions

• Charts and graphs of findings 

Discussion • Explanation of findings

• Interpretation of results

• Consideration of threats to internal validity 

Conclusions/ • Conclusions about program effectiveness

recommendations • Program recommendations 

Sections of report Content of sections

Table C.1 What to include in the evaluation report 11

11 Table from McKenzie and Smeltzer, Planning, Implementing, and Evaluating Health Promotion Programs: A Primer, 2nd ed. Copyright (c)

1997 by Allyn & Bacon. Adapted by permission.
C.2.2 Audience specificity

One of the key principles in communicating a

report is to tailor it to the audience. It should

have the audience’s level of education and

interests in mind. Key messages should be

formulated in the conclusion and abstract so that

they answer the questions most pertinent to the

audience. Conceivably you might have more

than one report - preparing both technical and

lay person versions is common. 

C.2.3 Clear language

The report should be written in clear language if

a non-technical audience is planned. This means

it will be quite different from the style found in

many academic publications. Guidelines for

clear language have been developed by many

organizations12. The following is a compilation

from some of these .

Appendix C

117

12 For example: Baldwin R [1990]. Clear writing and literacy. Toronto: ON Literacy Coalition; Canadian Labour Congress [1999]. Making it clear:

Clear language for union communications. Ottawa: Canadian Labour Congress; Gowers E (revised by Greenbaum S, Whitcut J) [1986]. The

complete plain words. London: HMSO; Ministry of Multiculturalism and Citizenship [1991]. Plain language clear and simple. Ottawa: Ministry of

Supply and Services.

Guidelines for writing in clear language

Overall

• Write with your audience’s needs, knowledge and abilities in mind

Document organization

• Include a table of contents for longer documents

• Divide document into sections of related information, using headings and sub-headings 

• Include detailed or technical material in an Appendix

Paragraphs

• Limit each paragraph to one idea

• Avoid paragraphs of more than five sentences

• Consider using point form for a list of related items

• Use left justification, but not right justification; i.e., leave a ragged right margin

Sentences

• Limit each sentence to one point

• Sentences should be no more than 20 words on average and, typically, not exceed 25 to 30 words

• Use a subject-verb-object order for most sentences

Words

• Avoid jargon and technical words; explain them when used 

• Eliminate unnecessary words (e.g., replace “in view of the fact” with “because”)

• Use the active voice instead of the passive voice. (e.g., replace “The requirement of the workplace

was that employees.....” with “The workplace required employees....)

• Avoid chains of nouns (e.g., resource allocation procedures)

Font

• Use a serif style of font (with hooks on the end of characters) instead of a sans serif style

• Do not use all upper case (i.e., all capital) letters for anything longer than a brief statement

• 12 point type is recommended for the main text
C.3 Communication beyond the

report

Communicating the evaluation results involves

more than producing the evaluation report.

Relationships between would-be users of the

evaluation results and the evaluators should be

established early on, because the successful

uptake of results often depends on a few key

individuals who understand and support the

evaluation. For this reason we recommend

forming an evaluation committee at the outset

that includes key stakeholders (Chapter 2). This

committee should be involved at all stages of the

evaluation: development of questions; selection

of design and methodology; and interpretation

of results. An ongoing engagement of

stakeholders fosters trust, understanding and

ownership of the results. It also helps ensure that

the results are appropriate to their needs. 

At the point of release of the final results, you

will ideally include several interactive means of

presenting the report’s results, involving either

larger verbal presentations or small group

meetings. Interaction of the audience with the

presenters should be encouraged in both cases.

Make sure the key messages of the report are

emphasized and give people the opportunity to

voice any doubts or lack of understanding. A

variety of written, verbal and visual presentations

might be needed for various audiences.

C.4 Summary

Communication of the evaluation results

involves, at the very least, a clear, wellorganized, audience-specific evaluation report.

Other strategies, including the ongoing

engagement of an appropriately structured

evaluation committee can further the use of an

evaluation’s results. 

Appendix C

118
Bibliography

Aday LA [1996]. Designing and conducting health surveys: a comprehensive guide. 2nd ed. San Francisco:

Jossey-Bass.

Altman DG [1991]. Practical statistics for medical research. London, New York: Chapman & Hall.

Armitage P, Berry G [1994]. Statistical methods in medical research. 3rd ed. Oxford, Boston: Blackwell

Scientific Publications. 

Becker MH, Haefner KP, Kasl SV, Kirscht JP, Maiman LA, Rosenstock IM [1977]. Selected psychosocial

models and correlates of individual health-related behaviors. Med Care 15:27-46.

Cherry N [1995]. Evaluation of preventive measures. In: McDonald C, ed. Epidemiology of work related

diseases. London: BMJ.

Clarke GM [1980]. Statistics & experimental design. London: Arnold.

Cohen J [1988]. Statistical power analysis for the behavioral sciences. New York: Academic Press.

Colton T [1974]. Statistics in medicine. Boston: Little, Brown & Company. 

Conrad KM, Conrad KJ, Walcott-McQuigg J [1991]. Threats to internal validity in worksite health

promotion program research: common problems and possible solutions. Am J Health Promot 6:112-122.

Cook TD, Campbell DT [1979]. Quasi-experimentation: design & analysis issues for field settings. Chicago:

Rand McNally College Publishing Co.

Cook TD, Campbell DT, Peracchio L [1990]. Quasi experimentation. In: Dunnette JD, Hough LM, eds.

Handbook of industrial and organizational psychology. 2nd ed., vol. 1. Palo Alto, CA: Consulting

Psychologists Press, Inc., pp. 491-576. 

Cresswell JW [1994]. Research design. Qualitative & quantitative approaches. Thousand Oaks, CA,

London, New Delhi: Sage Publications.

Dignan MB [1995]. Measurement and evaluation of health education. 3rd ed. Springfield, Illinois: Charles

C. Thomas.

Drummond MF, Stoddart GL, Torrance GW [1994]. Methods for the economic evaluation of health care

programmes. Oxford, Toronto, New York: Oxford University Press.

Earp JA, Ennett, ST [1991]. Conceptual models for health education research and practice. Health Educ

Res 6:163-171.

Fleiss JL [1981]. Statistical methods for rates and proportions, New York: John Wiley & Sons.

Bibliography

119
Freedman D, Pisani R, Purves R [1998]. Statistics. 3rd ed. WW Norton & Co.

Glassock DJ, Hansen ON, Rasmussen K, Carstensen O, Lauritsen J [1997]. The West Jutland study of

farm accidents: a model for prevention. Safety Sci 25:105-112.

Glendon I, Booth R [1995]. Risk management for the 1990s: Measuring management performance in

occupational health and safety. J Occup Health Safety - Aust NZ 11:559-565.

Gold RG, Siegel JE, Russell LB, Weinstein MC, eds. [1996]. Cost-effectiveness in health and medicine.

New York: Oxford University Press.

Goldenhar LM, Schulte PA [1994]. Intervention research in occupational health and safety. J Occ Med

36:763-775.

Goldenhar LM, Connally LB, Schulte PA, eds. [1996]. Intervention research in occupational health and

safety: science, skills and strategy. Special Issue of Am J Ind Med 29(4).

Green LW, Lewis FM [1986]. Measurement and evaluation in health education and health promotion.

California: Mayfield Publishing Co.

Greene JC, Caracelli VJ, Graham WF [1989]. Toward a conceptual framework for mixed-method evaluation

designs. Educ Eval & Policy Analysis 11:255-274.

Guastello SJ [1993]. Do we really know how well our occupational accident prevention programs work?

Safety Sci 16: 445-463.

Haddix AC, Teutsch SM, Shaffer PA, Dunet DO [1996]. Prevention effectiveness: a guide to decision

analysis and economic evaluation. Oxford, New York: Oxford University Press.

Hale AR [1984]. Is safety training worthwhile? J Occup Accid 6:17-33.

Hale AR, Glendon AI [1987]. Individual behavior in the control of danger. Amsterdam, New York: Elsevier.

Hale AR, Guldenmund F, Bellamy L [1999]. Annex 2: management model. In: Bellamy LJ, Papazoglou IA,

Hale AR, Aneziris ON, Ale BJM, Morris MI & Oh JIH I-Risk: Development of an integrated technical and

management risk control and monitoring methodology for managing and quantifying on-site and off-site

risks. Den Haag, Netherlands, Report to Ministry of Social Affairs and Employment, European Union,

Contract ENVA-CT96- 0243.

Hauer E [1980]. Bias-by-selection: Overestimation of the effectiveness of safety countermeasures caused

by the process of selection for treatment. Accid Anal Prev 12:113-117.

Hauer E [1986]. On the estimation of the expected number of accidents. Accid Anal Prev 18:1- 12.

Hauer E [1992]. Empirical Bayes approach to the estimation of “unsafety”: the multivariate regression

method. Accid Anal Prev 24:457-477.

Bibliography

120
Hawe P, Degeling D, Hall J [1990]. Evaluating health promotion: a health worker’s guide. Sydney,

Philadelphia, London, Australia: MacLennan & Petty.

Healey JF [1984]. Statistics: a tool for social research. Belmont: Wadsworth.

Hugentobler MK, Israel BA, Schurman SJ [1992]. An action research approach to workplace health:

integrating methods. Health Educ Q 19:55-76.

Johnston JJ, Cattledge GTH, Collins JW [1994]. The efficacy of training for occupational injury control.

Occup Med 9:147-158.

Kjellén U [1984]. The role of deviations in accident causation and control. J Occup Accidents 6:117-126. 

Kjellén U [2000]. Prevention of accidents through experience feedback. London, New York: Taylor &

Francis.

Kleinbaum DG, Kupper LL, Muller KE [1988]. Applied regression analysis and other multivariable

methods, 2nd ed. Boston: PWS-Kent.

Komaki JL, Jensen M [1986]. Within-group designs: an alternative to traditional control-group designs. In:

Cataldo MF, Coates TJ, eds. Health and industry: a behavioral medicine perspective. New York, Toronto,

Chichester, Brisbane, Singapore: John Wiley & Sons.

Komaki J, Barwick KD, Scott LR [1978]. A behavioral approach to occupational safety: pinpointing and

reinforcing safe performance in a food manufacturing plant. J Appl Psychol 63: 434-445.

Komaki J, Heinzmann AT, Lawson L [1980]. Effect of training and feedback: component analysis of a

behavioral safety program. J Appl Psychol 65: 261-270.

Krause TR [1995]. Employee-driven systems for safe behavior: integrating behavioral and statistical

methologies. New York: Van Nostrand Reinhold.

Laitinen H, Marjamaki M, Paivarinta K [1999a]. The validity of the TR safety observation method on

building construction. Accid Anal Prev 31:463-472.

Laitinen H, Rasa P-L, Resanen T, Lankinen T, Nykyri E [1999b]. The ELMERI observation method for

predicting the accident rate and the absence due to sick leaves. Am J Ind Med 1(Suppl):86- 88.

Lipsey MW [1990]. Design sensitivity. Newbury Park, CA: Sage Publications.

Mason ID [1982]. An evaluation of kinetic handling methods and training. [PhD thesis]. Birmingham:

University of Aston.

McAfee RB, Winn AR [1989]. The use of incentives/feedback to enhance work place safety: a critique of

the literature. J Safety Res 20:7-19.

Bibliography

121
McKenzie JF, Smeltzer JL [1997]. Planning, implementing, and evaluating health promotion programs: a

primer. 2nd ed. Boston: Allyn and Bacon.

Menckel E, Carter N [1985]. The development and evaluation of accident prevention routines: a case

study. J Safety Res 16:73-82.

Miles MB, Huberman AM [1994]. Qualitative data analysis. 2nd ed. Thousand Oaks, CA, London, New

Delhi: Sage Publications.

Mohr DL, Clemmer DI [1989]. Evaluation of an occupational injury intervention in the petroleum drilling

industry. Accid Anal Prev 21:263-271.

Morgan DL [1998]. Practical strategies for combining qualitative and quantitative methods: applications

to health research. Qual Health Res 8:362-376.

Morgan DL, Krueger RA [1998]. The focus group kit. Thousand Oaks, CA., London, New Delhi: Sage

Publications.

Needleman C, Needleman ML [1996]. Qualitative methods for intervention research. Am J Ind Med

29:329-337.

Norman GR, Streiner DL [1994]. Biostatistics: the bare essentials. St. Louis: Mosby.

Orgel DL, Milliron MJ, Frederick LJ [1992]. Musculoskeletal discomfort in grocery express checkstand

workers. J Occup Med 34:815-818.

Patton MQ [1986]. Utilization-focused evaluation. 2nd ed. Beverly Hills: Sage.

Patton MQ [1987]. How to use qualitative methods in evaluation. Newbury Park, CA, London, New

Delhi: Sage Publications.

Patton MQ [1990]. Qualitative evaluation and research methods. 2nd ed. Newbury Park, CA: Sage

Publications.

Pekkarinen A, Anttonen H, Pramila S [1994]. Accident prevention in reindeer herding work. Arctic 47:124-

127.

Reason J [1990]. Human error. Cambridge: Cambridge University Press.

Rivara FP, Thompson DC, eds. [2000]. Systematic reviews of strategies to prevent occupational injuries.

Special issue of Am J Prev Med 18(4)(Suppl).

Robins TG, Hugentobler MK, Kaminski M, Klitzman S [1990]. Implementation of the federal hazard

communication standard: does training work? J Occup Med 32:1133-1140.

Bibliography

122
Rossi PH, Berk RA [1991]. A guide to evaluation research theory and practice. In: Fisher A, Pavlova M,

Covello V, eds. Proceedings of the Evaluation and Effective Risk Communication Workshop. Interagency

Task Force on Environmental Cancer and Heart and Lung Disease Committe on Public Education,

EPA/600/9-90-054, pp. 205-254. 

Rush B, Ogborne A [1991]. Program logic models: expanding their role and structure for program planning

and evaluation. Can J Program Eval 6:95-106.

Siegel S, Castellan NJ Jr. [1988]. Nonparametric statistics for the behavioral sciences. 2nd ed. New York:

McGraw-Hill.

Sizing up safety: how to measure where your organization has been, where it’s at and where it’s going.

[1995]. Occup Health Safety 11(Mar/Apr):54-60

Steckler A, McLeroy KR, Goodman RM, Bird ST, McCormick L [1992]. Toward integrating qualitative

and quantitative methods: an introduction. Health Educ Q 19:1-8.

Stewart AL [1990]. Psychometric considerations in functional status instruments. In: Lipkin M Jr., ed.

Functional status measurement in primary care. New York: Springer-Verlag.

Streiner DL, Norman GR [1989]. Health measurement scales: a practical guide to their development and

use. Oxford: Oxford University Press.

Swinscow TDV [1978]. Statistics at square one. London: British Medical Association.

Tarrants WE [1987]. How to evaluate your occupational safety and health program. In: Slote L, ed.

Handbook of occupational safety and health. New York: John Wiley & Sons, ch. 8.

Vojtecky MA, Schmitz MF [1986]. Program evaluation and health and safety training. J Safety Res 17:57-

63.

Walsh NE, Schwartz RK [1990]. The influence of prophylactic orthoses on abdominal strength and low

back injury in the workplace. Am J Phys Med Rehabil 69:245-250.

Webb GR, Redman S, Wilkinson C, Sanson-Fisher RW [1989]. Filtering effects in reporting work injuries.

Accid Anal Prev 21:115-123.

Weinberg SL, Goldberg RP [1990]. Statistics for the behavioral sciences. Cambridge: Cambridge University

Press. 

Weiss CH [1988]. Evaluation for decisions: is anybody there? Does anybody care? Eval Practice 9:5-19.

Yin RK [1984]. Case study research: design and methods. Applied social research methods series. Vol. 5.

Beverly Hills, London, New Delhi: Sage Publications.

Zwerling C, Daltroy LH, Fine LJ, Johnston JJ, Melius J, Silverstein BA [1997]. Design and conduct of

occupational injury intervention studies: a review of evaluation strategies. Am J Ind Med 32: 164-179.

Bibliography

123
Bibliography

124