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TEACH-VIP

T rainin= g,

E ducating,

A dvancing

C ollaboration in

H ealth on

V iolence and

I njury

P revention =

Core curriculum

Lesson 7

= The materials in this lesson are based on an injury prevention and control curriculum originally = developed by the World Health = Organization and a global network = of injury experts.

Gen= eral lesson description

This l= ecture continues developing the general objective of the previous one. It offers explanations on analytic study designs including case-control studies, co= hort studies, and randomized controlled trials.

It exp= lains these designs by means of examples from the literature and explores potential u= ses, advantages and disadvantages of each methodology.

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General aspects on methods for studying and evaluating injury prevention, co= ntrol and safety promotion interventions

Studyi= ng injuries: research methods II

Lesson 7

Sessi= on time: 60 minutes

= Secti= on III. General epidemiological tools used = for injury prevention and control, and safety promotion

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Main objectiv= e of this lesson

=
To intr= oduce students to the fundamental principles of epidemiology and the methodologies used = in epidemiological research which can be applied to any field of injury pre= vention, control and safety promotion.

Core competen= cies that students should attain by the end of the session <= /div>
=

To gain an understa= nding of:

<= /span>

1. the design of an= alytical epidemiological studies of injury such as:

    observational studies including cross-sectional, case–control and cohort

    studies. <= /div>
2. intervention or experimental studies including quasi-experimental studies
    and randomized contro= lled trials;

3. the advantages, disadvantages and uses of the analytical study designs

    described;

4. the use of other= types of research such as systematic reviews and meta-

    analysis.

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Studying injuries:

research methods II

TEACH-VIP

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Analytic studies

Observational:

<= span style=3D'font-family:Arial;font-size:83%'>• cross-sectional studies

<= span style=3D'font-family:Arial;font-size:83%;visibility:hidden'>•<= /span> <= /span>

<= span style=3D'font-family:Arial;font-size:83%'>• case-control studies

<= span style=3D'font-family:Arial;font-size:83%;visibility:hidden'>•<= /span> <= /span>

<= span style=3D'font-family:Arial;font-size:83%'>• cohort studies <= /div>
<= span style=3D'font-family:Arial;font-size:83%;visibility:hidden'>•<= /span> <= /span>

<= span style=3D'font-family:Arial;font-size:83%'>• longitudinal studies <= /div>
<= span style=3D'font-family:Arial;visibility:hidden'>•

Intervention:

<= span style=3D'font-family:Arial;visibility:hidden'>•

<= span style=3D'font-family:Arial;font-size:83%'>• quasi-experimental studies

<= span style=3D'font-family:Arial;font-size:83%;visibility:hidden'>•<= /span> <= /span>

<= span style=3D'font-family:Arial;font-size:83%'>• randomized controlled trial (RCTs)=

Analyt= ical studies are designed to test one or more hypotheses. These studies usually focus = on an exposure (which frequently is a risk or protective factor for injuries= ), and its relation to a specific outcome or set of outcomes (injuries).

They c= an be used to evaluate treatments or prognosis as well as programmes and policies. These studies do not focus necessarily on injured people but can evaluate the effect of environmental modifications, implementation of laws or the establishment of community programmes.

They c= an be divided into two types of research designs: observational and intervention.

Obs= ervational studies include several research designs such as case-control studies, cohort studies, cross-sectional studies, and longitudinal designs.=

Int= ervention or experimental studies include randomized controlled trials (RCTs) and quasi-experimental studies.

The ma= in difference between an observational and an intervention study is that in the latter,= the researcher has control over the exposure or treatment status of the study subjects. This is useful to improve the validity of the comparisons made = in the study (1).

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Defined population

Gather data o= n risk or protective factors and injury

Injured

Not injured

Injured

Not injured

Four groups are = possible for each risk factor

Cross-sectional studies

Risk factor

No risk factor

The cross-sectional study examines the relationships between injuries (outcomes), and oth= er relevant variables (exposures or risk factors), as they exist in a defined population, at one particular point in time.

Althou= gh the cross-sectional study may reveal useful associations, because each subject’s status on both outcome and risk factor is determined at t= he same time, no causal inferences can be obtained from this design. Such an analysis can only suggest hypotheses regarding risk or protective factors= and is therefore rarely used for testing a cause-effect hypothesis.

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Children aged= 0-17 years in rural county

Risk factors:

age, sporting team participation, binge drinking

Injured

Not injured

Injured

Not injured

Four groups are = possible for each risk factor

Cross-sectional study applied

Binge drinking

No binge drinking

Example:

Source: Nordstrom e= t al., 2003.

The st= udy described in the slide investigated risk factors for non-fatal injury among rural children, aged 0–17 years, in Iowa, in the United States, using a cross-sectional survey (2).= The main risk factors associated with injury in this sample were age, members= hip of a sporting team, binge drinking and sedative use. Girls who binge dran= k or participated in team sports were more likely to be injured than boys who = did the same.

Object= ive

To ide= ntify risk factors for non-fatal injury among rural children.

Design=

Cross-= sectional health interview survey, 1994-98.

Settin= g

A rura= l Iowa county, not adjacent to a metropolitan area.

Subjec= ts

Strati= fied, random sample of households, including all resident children and adults.<= br>

Main o= utcome measures

Injury= episodes in the past 12 months among children aged 0–17 years and the parental = and child characteristics associated with these episodes.

Result= s

Of the= 621 children in participating households, 137 or 22.1% were injured during the past 12 months. Children aged 5–17 in a sports team were 1.88 times (95% confidence interval (CI) 1.07–3.31) more likely than other children= to be injured. Children aged 12–17 who binge drink were 3.50 times (95= % CI 1.31–9.50) more likely than other children to be injured. Compared = with children not in sports teams, girls in teams were 2.26 times (95% CI 1.02–5.13) more likely while boys in teams were 1.60 times (95% CI 0.71–3.68) more likely to have an injury episode. Compared with children who did not binge drink, girls binge drinking were 8.11 times (9= 5% CI 1.52–43.33) more likely while boys binge drinking were 2.19 time= s (95% CI 0.70–6.84) more likely to have an injury episode.

Conclu= sion

Local = studies such as this can provide useful clues regarding the etiology of injury. Some k= nown and some new potential risk factors including behavioural aspects for childhood non-fatal injury in a very rural area were investigated. It is planned to address these cross-sectional findings in future longitudinal follow up of this population.

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Advantages and disadvantages

Advantages:=

<= span style=3D'font-family:Arial'>• can reveal useful associations

= (i.e. binge drinking and injury)

Disadvantages:

• cannot infer causalit= y

Cross-sectional studies

The ma= in advantage of this design is that it can reveal useful associations, as in the examp= le on the previous slide, where an association was found between certain you= th behaviours such as binge drinking and the risk of injury.

As men= tioned before, the main disadvantage is that it is impossible to make inferences about causality based on temporal associations.

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Case-control studies

=

Bad <= /b>

outcome= 3;

(cases)= 3;

Good =

outcome= 3;

(controls)=

Not exposed

Exposed

Not exposed

Exposed

Source: adapted from Koepsell, 2= 001.

A case= -control study appears to approach testing a causal hypothesis backwards by proceeding f= rom effect to cause (see slide). The researcher begins by identifying persons= who have sustained an adverse outcome of interest (e.g. an injury) – the cases, and persons who did not experience the adverse outcome – the controls. The next stage is to gather information about the past exposure= of each group to the risk factor or factors of interest. Only exposure that preceded the outcome in cases (or a comparable “reference period= 221; in controls) is considered.

The re= sulting data can be analysed to estimate the strength and statistical significance of = the association between exposure and outcome. A case-control study may be eit= her retrospective or prospective in that the cases in a case-control study may have already experienced the outcome of interest when the study begins (retrospective), or they may be new cases that occur as the study proceeds (prospective) (1).

As men= tioned above, in a case-control study, a case may be an injured person and the control could be a person not injured. A case could also be a section of road whe= re a vehicle hit a tree and the control could be sections of road that the veh= icle traversed without hitting trees.

The re= search question here is how individual or environmental risk factors differ betw= een the cases and the controls.

This d= esign is often used for rare outcomes, such as injury, as it is very efficient. Cases and controls are selected and associations are established based upon potenti= al differences in exposures to one or more factors.

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Case-control study applied

Children presenting to hospital with an injury

(cases)

Children presenting to hospital for other conditions

(controls)=

Not exposed

Exposed

Not exposed

Exposed

Exposures related to:

lack of water supply =

low maternal education

poverty

crowding

Source: Delgado et al., 2002.

This e= xample of a case-control study was conducted in Lima, Peru by Delgado and colleagues = (3) to determine the risk factors associated with burns in children aged less than 18 years.

Cases = were defined as children who came to hospital with a burn injury. One control matched = for age and sex was selected for each case, from patients with other conditio= ns who presented at the same hospital.

A ques= tionnaire was administered to all consenting guardians of children admitted to the burns (cases) and general medicine (controls) units during a period of 14 month= s. Guardians of patients were questioned regarding etiology of the injury, demographic and socioeconomic data.

A tota= l of 740 cases and controls were enrolled. Altogether 77.5% of the cases burns occurred = in the patient's home, with 67.8% in the kitchen; 74% were due to scalding. = Most involved children younger than 5 years. Lack of water supply (odds ratio = (OR) 5.2, 95% confidence interval (CI) 2.1–12.3), low income (OR 2.8, 95= % CI 2.0–3.9), and crowding (OR 2.5, 95% CI 1.7–3.6) were associat= ed with an increased risk. The presence of a living room (OR 0.6, 95% CI 0.4–0.8) and better maternal education (OR 0.6, 95% CI 0.5–0.= 9) were protective factors.

It was= concluded that to prevent burns, interventions should be directed to low socioecono= mic status groups and these interventions should be designed according to loc= al risk factors.

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Advantages and disadvantages

Advantages:=

<= span style=3D'font-family:Arial'>• good for rare outcome= s

<= span style=3D'font-family:Arial'>• study of multiple risk factors

Disadvantages:

<= span style=3D'font-family:Arial'>• no information about absolute risks

Case-control studies

The ma= in advantage of a case-control study is that it is good for rare outcomes and ideal for studying multiple risk factors that preceded the injury outcome as seen in the previous example.

The ma= in disadvantage of a case-control study is that it cannot yield information = on absolute risk but only on relative risks of injury.

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Cohort studies

Identify study su= bjects

Measure and = classify exposure to r= isk factor(s)

Exposed

Not exposed

Bad outcome

Good outcome

Bad outcome

Good outcome

Source: adapted from Koepsell, 2= 001.

Study begins

Time=

Prospective stu= dy

Study begins

Time=

Retrospective study

The ke= y elements that define a cohort study are the designation of a population in which exposure status is known, then a period of time elapses, and one or more outcomes are observed or measured.

In a c= lassical cohort study, there are two cohorts: one exposed to the risk factor or factors under consideration and the other unexposed. The comparison focus= es on the measurement of good and bad outcomes related to the exposure.

These = studies can be prospective, meaning that at the beginning of the study no outcomes of interest (e.g. injuries) have occurred or retrospective, in which case exposures and events might have occurred but the researcher assembles the= two cohorts historically and follows them from the past towards the present.<= /font>

The di= agram above outlines the classical cohort study comparisons.

In the= field of injury epidemiology and prevention research, a cohort study may require injury as a criterion for membership of the cohort. Individuals are usual= ly identified from a medical facility and followed for outcomes of interest (e.g. disability). While these studies are essentially studies of prognos= is, they do not differ in principle from cohort studies of the cause of injury (4).

In all= observational studies an important issue to consider is the issue of confounding. Confounding relates to whether or not there are systematic differences between persons exposed versus those not exposed to a risk factor of interest. These systematic differences may be the source of the observed differences in outcome rather than exposure to the factor of interest.

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Cohort studies

Female = residents of = King County, Washington

Exposure to = intimate partner violence

Exposed:

filed for protection = order

Not exposed: did not file = for protection order

Hospitalized

Not hospitalized

Source: Kernic, Wolf & Holt, 2000.

Not = hospitalized

Hospitalized

Study begins

Time=

Retrospective stu= dy

The ex= ample shown here compares two groups of women within a population: those exposed to intimate partner violence and those not exposed (5).

In this retrospective cohort study, female residents of King County, Washington, = who had filed a civil protection order in 1992 were considered exposed to intimate partner violence. A comparison group consisted of women of the s= ame age who had not filed protection orders.

The ou= tcomes of interest in this case were overall and diagnosis-specific hospital admiss= ion rates and the relative risk of hospitalization associated with abuse in t= he 12-month period prior to seeking protection orders.

Object= ives

This s= tudy assessed the history of hospitalization among women involved in violent intimate relationships.

Method= s

In thi= s one-year retrospective cohort study, female residents of King County, Washington, = who were aged 18–44 years and who had filed for a protection order were compared with non-abused women in the same age group. Outcome measures included overall and diagnosis-specific hospital admission rates and rela= tive risk of hospitalization associated with abuse.

Result= s

Women = known to be exposed to a violent intimate relationship were significantly more likely= to be hospitalized with any diagnosis (age-specific relative risks (RRs) ran= ging from 1.2 to 2.1), psychiatric diagnoses (RR =3D 3.6, 95% confidence inter= val (CI) 2.8–4.6), injury and poisoning diagnoses (RR 1.8, 95% CI 1.2–2.8), digestive system diseases (RR 1.9, 95% CI 1.3–2.9),= and diagnoses of assault (RR 4.9, 95% CI 1.1–22.1) or attempted suicide= (RR 3.7, 95% CI 1.6–9.2) in the year before filing a protection order.<= /font>

Conclu= sion

This s= tudy showed an increased relative risk of both overall and diagnosis-specific hospitalizations among abused women. Intimate partner violence has a significant impact on women's health and use of health care.

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Advantages and disadvantages

Advantages:

• useful with common injuries and sh= ort follow-up

   (prospective)

• useful with rare exposures related= to an injury

• well-suited to studying multiple outcomes of the same        = ;

   exposure

• can be very effective in assessing effectiveness of

   interventions

• can also yield information about absolute level of risk

•

Disadvantages:

•<= /span> needs good data on exposures (often difficult in retrospective

studies)

• can be expensive (prospective)

Cohort studies

A p= rospective cohort study is useful when applied to injury problems that are common or that require a short follow-up, and can be useful in evaluating the effectiven= ess of an intervention. A prospective cohort study can, however, be very expensive if studying an uncommon outcome or if the follow-up period requ= ired to measure its incidence is long.

The co= hort study design is also useful for studying rare exposures, such as an unusual occupation or activity, as all available exposed individuals can form one cohort and a sample of the many unexposed individuals can form a comparis= on cohort.

Cohort= studies can also yield information about absolute level of risk (i.e. incidence estimates) for exposed and unexposed persons.

Ret= rospective cohort designs are also useful for studying outcomes that are relatively = rare where pre-existing information is available on large populations (e.g. Medicaid enrolees in the United States). In general, however, the feasibi= lity of a retrospective cohort study depends heavily on the availability of historical data (with details of the subjects’ exposure status at s= ome time in the past) and on having comparable follow-up data on exposed and unexposed subjects (1).

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Longitudinal studies

Before-after analysis

Injury

rate

Time

Intervention

Before=

After=

Longit= udinal studies incorporate repeated measurements of an outcome at the individual or group level over time. Changes in outcome are then evaluated in relation to kno= wn changes in one or several exposures.

The si= mplest design related to this is a before-after study that compares the frequency of an outcome (injury) in a group on two occasions: before and after the occurr= ence of a certain exposure. This exposure can be the passage of a law or the occurrence of an environmental change.

In the= hypothetical example above, a measurement of outcome (the rate of injury) is taken bef= ore and after an intervention is put in place. The graph suggests that there = has been a fall in injury rates since the intervention. However, a limitation= of the before-after design is that any differences observed may just represe= nt the continuation of an existing trend that was unrelated to the intervent= ion.

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Time-series analysis

Longitudinal studies

Injury

rate

Time

Intervention

Before=

After=

Some p= rotection against the possible misinterpretation of the results of a before-after s= tudy is offered by the interrupted time-series design. This involves taking several measures of the outcome frequency over time, both before and afte= r a new programme or policy is initiated. By taking multiple measures over ti= me, pre-existing trends can become apparent.

In the= example above, the presence of multiple measures of the injury rate over time mak= e it clear that the injury rate was actually increasing before the implementat= ion of the intervention, and that it began to decrease after the intervention. Based solely on the information in the before-after study (see previous slide), one could not be sure that the rate of injury was not already declining before the implementation of the intervention.

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Advantages and disadvantages

Advantages:=

• time-series can contr= ol for pre-existing trends

<= span style=3D'font-family:Arial'>• can evaluate the impa= ct of widely applied interventions

= such as laws or population-based programmes

• low cost (if existing= data used)

Disadvantages:

• before-after studies cannot contro= l for changes over time

= unrelated to the intervention of interest

Longitudinal studies

As men= tioned earlier, using multiple measurements of outcome over time can control for pre-existing secular changes.

Anothe= r advantage of these studies is that they can evaluate the effects of widely applied interventions (such as laws) and are usually low-cost if the data is alre= ady available from existing sources.

Before= -after studies may be subject to confounding from pre-existing secular trends and the results should therefore be treated with caution.

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Quasi-experimental studies

Subjects or <= /span>populations

Treatment (intervention)

Bad outcome

Control (comparison treatment)

= Non-random allocation

Good <= /span>outcome

Bad outcome

Good <= /span>outcome

The ty= pe of intervention study that does not involve random designation of subjects to comparison groups is termed a quasi-experiment. This is in contrast to the randomized controlled trial that is known as a true experiment.

This k= ind of study is usually conducted in the situation where a randomized controlled trial= is not possible. Assignment of the either the treatment (intervention) or control (comparison) group is non-random.

Althou= gh a quasi-experiment is an intervention study, it is more like an observation= al study than a randomized controlled trial in one important way. One cannot depend on the intervention and control groups being similar with regards = to other determinants of outcome. Therefore, attempts should always be made = to ensure that the intervention and control groups are as alike as possible = on certain key characteristics to avoid confounding.

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Content-Location: file:///C:/2D693CD7/CoreLesson7_files/slide0038.htm Content-Transfer-Encoding: quoted-printable Content-Type: text/html; charset="us-ascii" PowerPoint Presentation

Quasi-experimental study applied

Populations

Chicago:

Mandatory 7-day jail term for drink driving

Bad outcome

Milwaukee:

No mandatory jail <= span style=3D'position:absolute;top:58.75%;left:56.55%;width:32.02%;height:5.25= %'>sentence for drink = driving

= Non-random allocation

Reduced death rate from RTIs

Bad outcome

Reduced death rate from RTIs

Reduction in fatalities NOT due to difference in judicial policy

A quas= i-experiment is often employed to evaluate the effect of a programme, policy or regula= tion at the population level. Given that a law, for example, is enacted, the simplest question is whether it reduces injuries?

As we = have seen the simplest, but sometimes misleading, research design used to answer this question is to compare injury rates before and after the law is enacted. = If other factors are changing that would have increased or decreased injuries during the same period, the change in injury rate could be falsely attrib= uted to the law.

Robert= son (6) cites the example of the situation in the city of Chicago, in the United States, during the period 1970–71, when a supervising judge mandated a seven-day jail sentence for drunk driving. During this period the death r= ate declined and the rule was declared a success.

Aware = of the threats to validity in before-after comparisons, researchers designed a quasi-experimental study to examine the effects of Chicago’s judici= al policy. Comparisons of the death rates in Chicago and the nearby city of Milwaukee (which did not have a policy of mandatory jail sentences), duri= ng the same period, showed that a similar decline occurred at the same time = in Milwaukee. The reduced death rates were likely the result of recession in= the economy or changes in weather patterns that happened to occur at the same time as the judge’s sentencing policy.

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Randomized controlled trials

Subjects or <= /span>populations

Treatment (intervention)

Bad outcome

Control (comparison treatment)

= Random allocation

Good <= /span>outcome

Bad outcome

Good <= /span>outcome

The ra= ndomized controlled trial (RCT), which allocates individuals randomly to a treatme= nt (intervention) versus non-treatment (control or comparison) group, is the strongest type of design in the sense that it is the most effective in controlling for confounding. Random assignment of subjects to different treatment groups tends, on average, to balance the groups on other factors that could influence the outcome. It is , therefore, the best study design for actually obtaining a quantitative estimate of a causal association between an exposure or treatment and an outcome.

A simp= le two-group randomized design is shown above. Subjects are randomly assigned to one of two groups, here the treatment (or intervention) group and the control (or comparison) group. Often one treatment is experimental while the other ma= y be no treatment, a specific alternative treatment or usual care. Both groups= are then followed prospectively and the incidence of good and bad outcomes is measured and compared.

As the= design of choice among intervention studies, the RCT should be the first study desi= gn option considered for treatment and programme evaluations, resorting to o= ther less rigorous designs only if there are major obstacles to the RCT (1).

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Primary schools

Violence prev= ention curriculum

Less <= /span>= aggressive behaviours

Usual curriculum

Randomized

Behaviour not improved

Less <= /span>aggressive behaviours

Behaviour not improved

Randomized controlled trial applied

Source: Grossman et al., 1997.

This e= xample evaluates the effect of a violence prevention curriculum in the preventio= n of aggressive behaviours. Random allocation does not have to be exclusively = for individuals. In this case, schools were randomly allocated to receive or = not a violence prevention curriculum (7).

Object= ive

To det= ermine if a commonly used violence prevention curriculum, Second Step: A Violence Prevention Curriculum, leads to a reduction in aggressive behaviour and an increase in pro-social behaviour among elementary school students.=

Design=

Random= ized controlled trial.

Settin= g

Urban = and suburban elementary schools in the state of Washington.

Partic= ipants

Six ma= tched pairs of schools with 790 second-grade and third-grade students. The students were= 53% male and 79% white.

Interv= ention

The cu= rriculum uses 30 specific lessons to teach social skills related to anger management, impulse control and empathy.

Main o= utcome measures

Aggres= sive and pro-social behaviour changes were measured two weeks and six months after participation in the curriculum by parent and teacher reports (Achenbach Child Behavior Checklist and Teacher Report Form, the School Social Behav= ior Scale, and the Parent-Child Rating Scale), and by observation of a random sub-sample of 588 students in the classroom and playground or cafeteria settings.

Result= s

After = adjusting for sex, age, socioeconomic status, race, academic performance, household size and class size, the change in scores did not differ significantly between= the intervention and control schools for any of the parent-reported or teacher-reported behaviour scales. However, the behavioural observations = did reveal an overall decrease two weeks after the curriculum in physical aggression (P =3D 0.03) and an increase in neutral or pro-social behaviour (P =3D 0.04) in the intervention group compared with the control group. Most effects persisted six months later.

Conclu= sion

The Se= cond Step violence prevention curriculum appears to lead to a moderate observed decrease in physically aggressive beha= viour and an increase in neutral and pro-social behaviour in school.

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Advantages and disadvantages

Advantages:

<= span style=3D'font-family:Arial'>• “gold standard&= #8221; of epidemiological research

<= span style=3D'font-family:Arial'>• more likely than other designs to establish correct

= associations

<= span style=3D'font-family:Arial'>• less probability of b= ias and confounding

Disadvantages:

<= span style=3D'font-family:Arial'>• not applicable in all injury-related situations

• can be costly if used= to study rare or delayed outcomes

Randomized controlled trials

The RC= T is considered the “gold standard” of research design as it is mo= re likely than other designs to establish causal associations and is less li= kely to suffer from confounding and bias.

As wit= h prospective cohort studies and quasi-experiments, RCTs may be too expensive or impractical if the primary outcome of interest is rare, or if long period= s of follow-up are required before any intervention effects are apparent. Randomization may also be politically or morally unacceptable to collaborating organizations or individuals (random assignment of any protective device would raise serious ethical questions).

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Other types of research

Summary methods:&#= 13;

<= span style=3D'font-family:Arial;font-size:133%'>• review papers
=

<= span style=3D'font-family:Arial;font-size:133%'>• systematic reviews

<= span style=3D'font-family:Arial;font-size:133%;visibility:hidden'>•<= /span> =

<= span style=3D'font-family:Arial;font-size:133%'>• meta-analysis

There = are different methodologies for summarizing research. They range from a state-of-the-art review of a subject to systematic reviews that define certain parameters = for inclusion or exclusion of studies in order to facilitate comparability.

There = are more elaborate analyses such as the meta-analysis, which synthesizes the resul= ts of several studies that used the same methodology into one overall estima= te of association between exposures and outcomes.

These = methods are extremely useful as precursors to studies involving primary data collecti= on, as one should always have a firm grasp of the current state of knowledge about a specific injury subject, to be clear where the gaps are, before embarking on a new study.

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Purpose:

<= span style=3D'font-family:Arial'>• response to problems&= #13;

<= span style=3D'font-family:Arial'>• identification of best practice

<= span style=3D'font-family:Arial'>• evaluation of effecti= veness and cost-effectiveness

<= span style=3D'font-family:Arial;visibility:hidden'>•

Process:

• identify research que= stion (review literature)

<= span style=3D'font-family:Arial'>• choose appropriate st= udy design:

dependant on type of question asked

Summary

Descriptive:

• define magnitude

• identify risk factors

Analytic:

• test hypotheses

• establish relationships

Resear= ch should be aimed at responding to important social problems of concern to the commun= ity, and should contribute to the identification of best practice through the evaluation of treatments, programmes or policies.

To sum= marize, the first step in any research project is to ask a question or state a hypothesis. To find out what needs to be known, one must first find out w= hat is already known by reviewing the literature.

The ch= oice of research study design will then depend on the question being asked. Some research simply attempts to describe the current state of affairs, without any expectation about what might be found. For example, what are the most common injuries associated with motorcycle crashes? How common are burns = and scalds among preschool children? This kind of research is typically best addressed by a descriptive study (1). The type of descriptive study chosen will depend on the nature of the question and the nature of the data available.

In con= trast, other studies seek to test a specific hypothesis. Often the research question f= or an analytical study is whether a certain cause (which may be an intervent= ion) leads to a certain effect. For example, does a programme to prevent falls= in the elderly significantly reduce the incidence of falls? Do bicycle helme= ts protect wearers against head injury in the event of an accident? These ki= nds of questions are usually best addressed by an analytical study design (1). The type of analytical study design chosen will again depend on the natur= e of the question, the potential to manipulate exposure or treatment by the investigator, the frequency of the outcome of interest and opportunities = or barriers (e.g. resources availability) that may exist locally.

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General lesson description
This lecture conti= nues developing the general objective of the previous one. It offers explanations on analytic study designs including case-control studies, cohort studies, and randomized controlled trials. It explains these designs by means of examples from the literature and explores potential uses, advantages and disadvantages of each methodology.

Analytical studies are designed to test one or more hypotheses. The= se studies usually focu= s on an exposure (which frequently is a risk or protective factor for injuries), and its relation to a specif= ic outcome or set of outcomes (injuries). They can be used to evaluate treatments= or prognosis as well as programmes and policies. These studies do not focus necessarily on injured peo= ple but can evaluate the effect of environmental modifications, implementation of laws or the establishment of community programmes. They can be divided into two types of research designs: observational and intervention. Observational studies include several research designs such = as case-control stud= ies, cohort studies, cross-sectional studies, and longitudinal designs. Intervention or experimental studies= include randomized controlled trials <= /span>(RCTs) and quasi-experimental studies.&= #13;The main difference between an observational and an intervention study is that in the latter, the researcher has control over the exposure or treatment status of the study subjects. This is useful to improve the validity of the comparisons made in the study (1). = ;

The cross-sec= tional study examines the relationships between injuries (outcomes), and other relevant variables (exposures or risk factors= ), as they exist in a defined population, at one particular point in time. Although the cross-sectional study may reveal useful associations, because each subject’s status on both outcome and risk factor is determined at the same time, no causal inferences can be obtained from this design. Such an analysis can only suggest hypotheses regarding risk or protective factors and is therefore rarely used for testing a cause-effect hypothesis.

The study described in the slide investigated risk factors for non-fatal injury among rural children, aged 0–17 years, = in Iowa, in the United States, using a cross-sectional survey&nb= sp; (2). The main risk factors associated with injury in this sample were age, membersh= ip of a sporting team, binge drinking and sedative use. Girls who binge drank= or participated in team spor= ts were more likely to be injured than boys who did the same.
Obje= ctive

To identify risk factors for non-fatal injury among rural children.

Desi= gn

Cros= s-sectional health interview survey, 1994-98.

Sett= ing

A ru= ral Iowa county, not adjacent to a metropolitan area.

Subj= ects

Stra= tified, random sample of households, including all resident children and adults.

Main outcome measures
Inju= ry episodes in the past 12 months among children aged 0–17 years and the parental and child characteristics associated with these episodes.
Resu= lts
Of t= he 621 children in participating households, 137 or 22.1% were injured during= the past 12 months. Children aged 5–17 in a sports team were 1.88 times (95% confidence interval (CI) 1.07–3.31) more likely than other children to be injured. Children aged 12–17 who binge drink were 3.50 times (95% CI 1.31–9.50) more likely than other children to be injured. Compared with children = not in sports teams, girls in teams were 2.26 times (95% CI 1.02–5.13) more lik= ely while boys in teams were 1.60 times (95% CI 0.71–3.68) more likely to have an injury more likely while boys binge drinking were 2.19 times (95% CI 0.70–6.84) more likely to have an injury episode.
Conc= lusion
Local studies such as this can provide useful clues regarding the etiology of injury. Some known and some new potential risk factors including behavioural aspects = for childhood non-fatal injury in a very rural area were investigated. It is plann= ed to address these cross-sectional findings in future longitudinal follow up= of this
The main advantage of this design is that it can reveal useful associations, as in the example on the previous slide, where an association was found between certain youth behaviours such as binge drinking and the risk of injury. As mentioned before, the main disadvantage is that it is impossible= to make inferences about causality based on temporal associations.

A case-control study appears to approach testing a causal hypothesi= s backwards by proceeding from effect to cause (see slide). The researcher begins by identifying persons who have sustained an adverse outcome= of interest (e.g. an injury) – the cases, and persons who did not experience the adverse outcome – the controls. T= he next stage is to gather information about the past exposure of each group to the risk factor or factors= of interest. Only exposure that preceded t= he outcome in cases (or a comparable “reference period” in controls) is considere= d. The resulting data can be analysed to estimate the strength and statistical significance of the association between exposure and outcome. A case-control study may be either retrospective or prospective in that the cases in a case-contr= ol study may have already experienced the outcome of interest when the study begins (retrospective), = or they may be new cases that occur as the study proceeds (prospective) (1). As mentioned above, in a case-control study, a case may be an injured person and the control could be a person not injured. A case could = also be a section of r= oad where a vehicle hit a tree and the control could be sections of road that the vehicle traversed with= out hitting trees. The research question here is how individual or environmental risk factors differ betwe= en the cases and the controls. This design is often used for rare outcomes, such as injury, as it = is very efficient. C= ases and controls are selected and associations are established based upon potential differences in exposures to one or more factors.

This example of a case-control study was conducted in Lima, Peru by= Delgado and colleagues (3) to determine= the risk factors associated with burns in children aged less than 18 years.

Cases were defined as children who came to hospital with a burn inj= ury. One control matched for age and sex was selected for each case, from patients with other conditions who presented at the same hospital.

A questionnaire was administered to all consenting guardians of children admitted to = the burns (cases) and general medicine (controls) units during a period of 14 months. Guardians of patie= nts were questioned regarding etiology of the injury, demographic and socioeconomic data.

A total of 740 cases and controls were enrolled. Altogether 77.5% of the cases burns occurred in the patient's home, with 67.8% in the kitchen; 74% were due to scalding. Most involved children younger than 5 years. Lack of water supply (odds ratio (OR) 5.2, 95% confidence interval (CI) 2.1–12.3), low income (OR 2.8, 95% CI 2.0–3.= 9), and crowding (OR 2.5, 95% CI 1.7–3.6) were associated with an increased risk. The presence of a living room (OR 0.6, 95% CI 0.4–0.8) and better maternal education (OR 0.= 6, 95% CI 0.5–0.= 9) were protective factors. = 3;

It was concluded that to prevent burns, interventions should be directed to low socioeconomic status groups and these interventions should be designed according to local risk factor= s.

The main advantage of a case-control study is that it is good for r= are outcomes and ideal for studying multiple risk factors that preceded the injury outcome as seen in the previous example. The main disadvantage of a case-control study is that it cannot yield information on absolute risk but only on relative risks of injury.

The key elements that define a cohort study are the designation of a population in which exposure status is known, then a period of time elaps= es, and one or more outcomes are observed or measured. In a classical cohort stu= dy, there are two cohorts: one exposed to the risk factor or factors under consideration and t= he other unexposed. The comparison focuses on the measurement of good and b= ad outcomes related to the exposure. These studies can be prospective, meaning that at the beginning of the study no outcomes of interest (e.g. injurie= s) have occurred or retrospective, in which case exposures and events might have occurred but the researcher assembles the two cohorts historically and follows them from the past towards the present.
The diagram above outlines the classical cohort study comparisons.
In t= he field of injury epidemiology and prevention research, a cohort study may require injury In all observational studies an important issue to consider is the issue of confounding. Confounding relates to whether or not there are systematic differences between persons exposed versus those not exposed to a risk factor of interest. These systematic differences = may be the source of the observed differences in outcome rather than exposure to the factor of interest.

The example shown here compares two groups of women within a population: those exposed to intimate partner violence= and those not exposed (5). = In this retrospective coh= ort study, female residents of King County, Washington, who had filed a civil protection order in 1992 were considered exposed to intimate partner violence. A comparison group consisted of women = of the same age who had not filed protection orders. The outcomes of interest = in this case were overall and diagnosis-specific hospital admission rates and the relative risk of hospitalization associated with abuse in the 12-month period prior to seek= ing protection orders.
Obje= ctives
This study assessed the history of hospitalization among women involved in viol= ent intimate Meth= ods
In t= his one-year retrospective cohort study, female residents of King County, Washington, who were aged 18–44 years and who had filed for a protec= tion order were compared with non-abused women in the same age group. Outcome measures included overall and diagnosis-specific hospital <= span lang=3DEN-GB style=3D'font-family:Arial;mso-ascii-font-family:Arial;mso-bi= di-font-family: Arial;mso-hansi-font-family:Arial;font-size:83%'>admission rates and relat= ive risk of hospitalization associated with abuse.
Resu= lts
Women known to be exposed to a violent intimate relationship were significantly = more likely to be diagnoses of assault (RR 4.9, 95% CI 1.1–22.1) = or attempted suicide (RR 3.7, 95% CI 1.6–9.2) in the year before filing a protection order.
Conc= lusion
This study showed an increased relative risk of both overall and diagnosis-spec= ific hospitalizations

A prospecti= ve cohort study is useful when applied to injury problems that are common or that require a short follow-up, and can be useful in = evaluating the effectiveness of an intervention. A prospective cohort study can, however, be very expensive if stud= ying an uncommon outcome or if the follow-up period required to measure its incidence is long. The cohort study design is also useful = for studying rare exposures, such as an unusual occupation or activity, as all available exposed individ= uals can form one coh= ort and a sample of the many unexposed individuals can form a comparison cohort. Cohort studies can also yield informati= on about absolute<= /b> level of risk (i.e. incidence estimates) for exposed and unexposed persons. = Retrospective cohort designs are also useful for studying outcomes that are relatively rare where pre-existing information is available on large populations (e.g. Medicaid enrolees in the United States). In general, however, the feasibility of a retrospec= tive cohort study depends heavily on the availability of historical data (with details of the subjects’ exposure status at some time in the past) and on having comparable follow-up data o= n exposed and unexposed subjects (1).

Longitudinal studies incorporate repeated measurements of an outcom= e at the individual or group level over time. Changes in outcome are then evaluated in relation to known changes = in one or several exposures. The simplest design related to this is a before-after study that compares the frequency of= an outcome (injury) in a group on two occasions: before and after the occurrence of a certain expos= ure. This exposure can be the passage of a law or the occurrence of an environmental change. = ;In the hypothetical example above, a measurement of outcome (the rate of injury) is taken before and after an intervention is put in place. = The graph suggests that there has been a fall in injury rates since the intervention. However, a limitation of the before-aft= er design is that any differences observed may just represent the continuation of an existing trend t= hat was unrelated to= the intervention.

Some protection against the possible misinterpretation of the resul= ts of a before-after study is offered by the interrupted time-series design. This involves taking several measures of the outcome frequency over time, both before and after a new programme or policy is initiated. By taking multiple measures over time, pre-existing trends can become apparent. In the example above, the presence of multiple measures of the injury rate over time make it clear that the injury rate was actually increasing before the implementation of the intervention, and that it began to decrease after the intervention. Based solely on the information in the before-after study (see previous slide), one could not be = sure that the rate of injury was not already declining before the implementation of the intervention.

As mentioned earlier, using multiple measurements of outcome over t= ime can control for pre-existing secular changes. Another advantage of these studies is that they can evaluate the effects of widely applied interventions (such as l= aws) and are usually low-cost if the data is already available from existing sources. Before-after studies may be subject to confounding from pre-existing secular trends and the results should therefore be treated with caution.

The type of intervention study that does not involve random designa= tion of subjects to comparison groups is termed a quasi-experiment. This is in contrast to the randomized controlled t= rial that is known as a true experiment. This kind of study is usually conducted in the situation where a randomized controlled t= rial is not possible. Assignment of the either the treatment (intervention) or control (comparison) group is non-random. Although a quasi-experiment is an intervention study, it is more li= ke an observational study than a randomized controlled trial in one important way. One cannot depend on the intervention a= nd control groups being similar with regards to other determinants of outcome. Therefore, attempts shoul= d always be made to ensure that the intervention and control groups are as alike as possible on certain key characteristics to avoid confounding.

A quasi-experiment is often employed to evaluate the effect of a programme, policy or regulation at the population level. Given that a law, for example, is enacted, the simplest question is wheth= er it reduces injuries? As we have seen the simplest, but sometimes misleading, research de= sign used to answer this question is to compare injury rates before and after the law is enacted. If other factors are changing that would have increased or decreased injuries during the same peri= od, the change in injury rate could be falsely attributed to the law. Robertson (6) cites the example of the situation in the city of Chicago, in the United States, during the period 1970–71, when a supervising judge mandated a seven-day jail sentence for drunk driving. During this period the death rate declined and the rule was declared a success. Aware of the threats to validity in before-after comparisons, researchers designed a quasi-experimental study to examine the effects of Chicago’s = judicial policy. Comparisons of the dea= th rates in Chicago and the nearby city of Milwaukee (which did not have a policy of mandatory jail sentenc= es), during the same period, showed that a similar decline occurred at the same time in Milwaukee. The reduced death ra= tes were likely the result of recession in the economy or changes in weather patterns that happen= ed to occur at the same time as the judge’s sentencing policy.

The randomized controlled trial (RCT), which allocates individuals randomly to a treatme= nt (intervention) versus non-treatment (control or comparison) group, is the strongest type of design = in the sense that it is the most effective in controlling for confounding. Random assignment of subj= ects to different treatment groups tends, on average, to balance the groups on other factors that could influence the outcome. It is , therefore, the best study design for actually obtaining a quantitative estimate of a ca= usal association betwee= n an exposure or treatment and an outcome. A simple two-group randomized design is shown above. Subjects are randomly assigned to one of two groups, here the treatment (or intervention) group and the control (or comparison) group. Often one treatment is experimental while the other may be no treatment, a specific alternative treatment or usual care. Both groups are then followed prospectively and the incidenc= e of good and bad outcomes is measured and compared. As the design of choice among intervent= ion studies, the RCT should be the first study design option considered for treatment and programme evaluations, resorting to other less rigorous designs only if there are major obstacles to the RCT (1).

This example evaluates the effect of a violence prevention curriculum in the prevention of aggressive behaviours. Random <= /span>allocation does not have = to be exclusively for individuals. In this case, schools were randomly alloca= ted to receive or not a violence prevention curriculum (7).
Obje= ctive
To determine if a commonly used violence prevention curriculum, Second Step: A Violence Prevention Curriculum, leads to a reduction in aggressive behaviour and an increase in pro-social behaviour among elementary school students.
Desi= gn

Rand= omized controlled trial.

Sett= ing

Urban and suburban elementary schools in the state of Washington.
Part= icipants

Six matched pairs of schools with 790 second-grade and third-grade students. T= he students were 53% male and 79% white.

Inte= rvention

The curriculum uses 30 specific lessons to teach social skills related to anger management, impulse control and empathy.

Main outcome measures
Aggr= essive and pro-social behaviour changes were measured two weeks and six months af= ter participation in the curriculum by parent and teacher reports (Achenbach Child Behavior Checklist and Teacher Report Form, the School Social Behavior Scale, and the Parent-Child Rati= ng Scale), and by observation of a random sub-sample of 588 students in the classroom and Resu= lts
After adjusting for sex, age, socioeconomic status, race, academic performance, household size and class size, the change in scores did not differ significantly between the intervention and control schools for any of the parent-reported or teacher-reported behaviour scales. However, the behavioural observatio= ns did reveal an overall decrease two weeks after the curriculum in physical aggression (P =3D 0.03) and an increase= in neutral or pro-social behaviour (P =3D 0.04) in the intervention group compared <= span lang=3DEN-GB style=3D'font-family:Arial;mso-ascii-font-family:Arial;mso-bi= di-font-family: Arial;mso-hansi-font-family:Arial;font-size:75%'>with the control group. M= ost effects persisted six months later.
Conc= lusion
The Second Step violence prevention curriculum appears to lead to a moderate observed decrease in physically aggressive behaviour and an increase in neutral and pro-social behaviour in school.

The RCT is considered the “gold standard” of research design as it is more likely than other designs to establish causal associations and is l= ess likely to suffer from confounding and bias. As with prospective cohort studies and quasi-experiments, RCTs may = be too expensive or impractical if the pri= mary outcome of interest is rare, or if long periods of follow-up are required before any intervention effe= cts are apparent. Randomization may also be politically or morally unacceptable to collaborating organizations or individu= als (random assignment of any protective device would raise serious ethical questions).
There are different methodologies for summarizing research. They ra= nge from a state-of-the-art review of a sub= ject to systematic reviews that define certain parameters for inclusion or exclusion of studies in order to facilitate comparabilit= y. There are mo= re elaborate analyses such as the meta-analysis, which synthesizes the results of several stud= ies that used the same methodology into one overall estimate of association between exposures and outcomes. These methods are extremely useful as precursors to studies involving primary data collection, as one should always have a firm grasp of the current state of knowledge about a specific injury subject, to be c= lear where the gaps are, before embarking on a new study.

Research should be aimed at responding to important social problems= of concern to the community, and should contribute to the identification of best practice through the evaluation of treatments, programmes or policies.

To summarize, the first step in any research project is to ask a question or state a hypothesis. To find out what needs to be known, one must first find out what is already known by reviewing = the literature.

The choice of research study design will then depend on the question being asked. Some research simply attempts to describe the current state of affairs, without any expectation about = what might be found. For example, what are the most common injuries associated with motorcycle crashe= s? How common are burns and scalds among preschool children? This kind of research is typically best addressed by a descriptive study (1). The type of descriptive study chosen will depend on the nature of the question and the nature of the data available.

In contrast, other studies seek to test a specific hypothesis. Often the research question for an analytical study is whether a certain cause (which = may be an intervention) leads to a cert= ain effect. For example, does a programme to prevent falls in the elderly significantly reduce the incidence of falls? Do bicycle helmets protect wearers against head injury in the event of an accident? These kinds of questions are usually best addressed by an analytical study design (1). The type of analytical study design ch= osen will again depend= on the nature of the question, the potential to manipulate exposure or treatment by the investigat= or, the frequency of the outcome of interest and opportunities or barriers (e.g. resources availability) that may exist locall= y.

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UpdNavPane( sldIndex ){ if(gNavLoaded) PPTNav.UpdNav() } function UpdOtNavPane(){ if(gOtlNavLoaded) PPTOtlNav.UpdOtlNav() } function UpdOtlPane(){ if(gOtlLoaded) PPTOtl.UpdOtl() } function SetHasNts( fVal ) { if( gHasNts !=3D fVal ) { gHasNts=3DfVal UpdNavPane() } } function ToggleOtlText() { gOtlTxtExp=3D!gOtlTxtExp UpdOtlPane() } function ClearMedia() { // Clear any sounds playing before launching another browser window. Other= wise, // in fullscreen mode, you'll continue to hear the sound in the frames mod= e. if (PPTSld.pptSound) PPTSld.pptSound.loop =3D 0; } function FullScreen() {=20 if ( PPTSld.g_animUseRuntime ) PPTSld.document.body.pause(); ClearMedia(); var href =3D ( document.location.protocol =3D=3D 'mhtml:') ? FULLSCR_HREF = : FULLSCR_HREF+"#"+GetHrefObj(gCurSld).mSldHref; if (MHTMLPrefix !=3D "") href =3D RemoveFilePrefixFromHref(href) if(PPTNav.event.ctrlKey) { var w =3D (window.screen.availWidth * 1.0) / 2.0 var h =3D w * (PPTSld.g_origH * 1.0) / PPTSld.g_origW win =3D window.open( MHTMLPrefix+href,null,"toolbar=3D0,resizable=3D1,top= =3D0,left=3D0," + "width=3D"+ w + ",height=3D" + h ); if( win.document.body && PPTSld.g_animUseRuntime ) win.document.body.PPTSldFrameset=3Dwindow; } else { win =3D window.open( MHTMLPrefix+href,null,"fullscreen=3Dyes" ); if( win.document.body && PPTSld.g_animUseRuntime ) win.document.body.PPTSldFrameset=3Dwindow; } } function ToggleVNarration() { rObj=3DPPTSld.document.all("NSPlay") if( rObj && !PPTSld.g_animUseRuntime ) { if( (rObj.playState =3D=3D 1)||(rObj.playState =3D=3D 0) ) rObj.Play() else if( rObj.playState =3D=3D 2 ) rObj.Pause() else return; } else if( PPTSld.g_animUseRuntime ) { narObj =3D PPTSld.document.all("narrationID") if( narObj ) narObj.togglePause() } } function GetCurSldNum() { =20 obj=3DGetHrefObj(gCurSld) if( obj.mOrigVis =3D=3D 1 ) return obj.mSldIdx else =20 return gCurSld } function GetNumSlds() { =20 if( GetHrefObj(gCurSld).mOrigVis =3D=3D 1 ) return GetSldList().mNumVisSlds; else return GetSldList().mList.length } function GetSldNum( href ) { for(ii=3D0; ii 1 ) PopSldList(); else if( !IsFramesMode() ) { if( gLoopCont ) GoToFirst() else EndShow() } } function GoToPrevSld() { ii=3DgCurSld-1 if( ii > 0 ) { obj=3DGetHrefObj(ii) while ( obj && ( obj.mVis =3D=3D 0 ) && ( ii>0 ) ) obj=3DGetHrefObj(--ii) if( ii =3D=3D 0 ) ii=3D1 GoToSldNum(ii) } } function GoToFirst(){ GoToSld( GetHrefObj(1).mSldHref ) } function GoToLast() { ii=3DGetSldList().mList.length if( ii !=3D gCurSld ) GoToSld( GetHrefObj(ii).mSldHref ) } function GoToSldNum( num ) { if( PPTSld.event ) PPTSld.event.cancelBubble=3Dtrue obj =3D GetHrefObj( num ) obj.mVis=3D1 gPrevSld=3DgCurSld gCurSld =3D num; =09 if (MHTMLPrefix !=3D "") PPTSld.location.replace(MHTMLPrefix+RemoveFilePrefixFromHref(obj.mSldHref= )) else PPTSld.location.replace(obj.mSldHref) =09 if( IsFramesMode() ) { UpdNavPane(); UpdOtlPane(); UpdNtsPane() } } function GoToSld( href ) { if( PPTSld.event ) PPTSld.event.cancelBubble=3Dtrue GetHrefObj( GetSldNum(href) ).mVis=3D1 if (MHTMLPrefix !=3D "") PPTSld.location.replace(MHTMLPrefix+RemoveFilePrefixFromHref(href)) else PPTSld.location.replace(href) } function SldUpdated( id ) { if( id =3D=3D GetHrefObj(gCurSld).mSldHref ) return gPrevSld=3DgCurSld gCurSld=3DGetSldNum(id) if( IsFramesMode() ) { UpdNavPane(); UpdOtlPane(); UpdNtsPane() } } function PrevSldViewed(){ GoToSld( GetHrefObj(gPrevSld).mSldHref ) } function HasPrevSld() { return ( gIsEndShow || ( gCurSld !=3D 1 && GetHrefO= bj( gCurSld-1 ).mVis =3D=3D 1 )||( GetCurSldNum() > 1 ) ) } function HasNextSld() { return (GetCurSldNum() !=3D GetNumSlds()) } function CloseWindow() { if( HideMenu() ) return; =09 var event =3D PPTSld.event; if( !IsFramesMode() && event && (event.keyCode=3D=3D27 || event.keyCode=3D= =3D32 || event.type=3D=3D"click" ) ) window.close( self ); CatchNumKeys( self, event ); } function Unload() { gIsEndShow=3D0; } function SetupEndShow() { gIsEndShow=3D1; PPTSld.document.body.scroll=3D"no"; PPTSld.document.onkeypress=3DCloseWindow; PPTSld.document.onclick=3DCloseWindow; PPTSld.document.oncontextmenu=3D_CM; } function EndShow() { if( IsFramesMode() ) return if( PPTSld.event ) PPTSld.event.cancelBubble=3Dtrue doc=3DPPTSld.document var dir =3D doc.body.dir if( dir !=3D "rtl" ) dir =3D "ltr"; doc.open() doc.writeln('

' + ENDSHOW_MESG + '
') doc.close() } function SetSldVisited(){ GetSldList().mList[gCurSld-1].mVisited=3Dtrue } function IsSldVisited(){ return GetSldList().mList[gCurSld-1].mVisited } function hrefList( sldHref, visible, advDelay, advClk ) { this.mSldHref=3D this.mNtsHref =3D sldHref this.mOrigVis=3D this.mVis =3D visible this.mVisited=3D false this.mAdvDelay=3D advDelay this.mAdvOnClk=3D advClk } function SldList(arr,curSld,fEnd) { this.mCurSld =3D curSld; this.mList =3D new Array(); var idx =3D 1; for(ii=3D0;ii 0) { PushSldList(sldList,fEnd); gCurSld =3D 1; } else if( PPTSld.event ) PPTSld.event.cancelBubble=3Dtrue } function PushSldList(arr,fEnd) { var ii =3D gSldStack.length; gSldStack[ii] =3D new SldList(arr,gCurSld,fEnd); GoToSld( gSldStack[ii].mList[0].mSldHref ); } function PopSldList() { if (gSldStack[gSldStack.length-1].fEndShow) EndShow() else { gCurSld =3D gSldStack[gSldStack.length-1].mCurSld; gSldStack[gSldStack.length-1] =3D null; gSldStack.length--; var sldList =3D gSldStack[gSldStack.length-1]; GoToSld( sldList.mList[gCurSld - 1].mSldHref ); } } var custShowList=3Dnew Array(); /********************************************* Navigation button implementation There are 2 types of buttons: ImgBtn, TxtBtn implemented as function objects. They share a similiar interface so the event handlers can call SetActive, for example, on a button=20 object without needing to know exactly=20 what type of button it is. **********************************************/ //---------------------------------- function ImgBtn( oId,bId,w,action ) //---------------------------------- { var t=3Dthis t.Perform =3D _IBP t.SetActive =3D _IBSetA t.SetInactive=3D _IBSetI t.SetPressed =3D _IBSetP t.SetDisabled=3D _IBSetD t.Enabled =3D _IBSetE t.ChangeIcon =3D null t.UserAction =3D action t.ChgState =3D _IBUI t.mObjId =3D oId t.mBorderId=3D bId t.mWidth =3D w t.mIsOn =3D t.mCurState =3D 0 } function _IBSetA() { if( this.mIsOn ) { obj=3Dthis.ChgState( gHiliteClr,gShadowClr,2 ) obj.style.posTop=3D0 } } function _IBSetI() { if( this.mIsOn ) { obj=3Dthis.ChgState( gFaceClr,gFaceClr,1 ) obj.style.posTop=3D0=20 } } function _IBSetP() { if( this.mIsOn ) { obj=3Dthis.ChgState( gShadowClr,gHiliteClr,2 ) obj.style.posLeft+=3D1; obj.style.posTop+=3D1 } } function _IBSetD() { =20 obj=3Dthis.ChgState( gFaceClr,gFaceClr,0 ) obj.style.posTop=3D0=20 } function _IBSetE( state ) { var t=3Dthis GetObj( t.mBorderId ).style.visibility=3D"visible" if( state !=3D t.mIsOn ) { t.mIsOn=3Dstate if( state ) t.SetInactive() else t.SetDisabled() } } function _IBP() { var t=3Dthis if( t.mIsOn ) { if( t.UserAction !=3D null ) t.UserAction() if( t.ChangeIcon ) { obj=3DGetObj(t.mObjId) if( t.ChangeIcon() ) obj.style.posLeft=3Dobj.style.posLeft+(t.mCurState-4)*t.mWidth else obj.style.posLeft=3Dobj.style.posLeft+(t.mCurState-0)*t.mWidth } t.SetActive() } =20 } function _IBUI( clr1,clr2,nextState ) { var t=3Dthis SetBorder( GetObj( t.mBorderId ),clr1,clr2 ) obj=3DGetObj( t.mObjId ) obj.style.posLeft=3Dobj.style.posLeft+(t.mCurState-nextState)*t.mWidth-obj= .style.posTop t.mCurState=3DnextState return obj } //----------------------------------------- function TxtBtn( oId,oeId,action,chkState ) //----------------------------------------- { var t=3Dthis t.Perform =3D _TBP t.SetActive =3D _TBSetA t.SetInactive=3D _TBSetI t.SetPressed =3D _TBSetP t.SetDisabled=3D _TBSetD t.SetEnabled =3D _TBSetE t.GetState =3D chkState t.UserAction =3D action t.ChgState =3D _TBUI t.mObjId =3D oId t.m_elementsId=3D oeId t.mIsOn =3D 1 } function _TBSetA() { var t=3Dthis if( t.mIsOn && !t.GetState() ) t.ChgState( gHiliteClr,gShadowClr,0,0 ) } function _TBSetI() { var t=3Dthis if( t.mIsOn && !t.GetState() ) t.ChgState( gFaceClr,gFaceClr,0,0 ) } function _TBSetP() { if( this.mIsOn ) this.ChgState( gShadowClr,gHiliteClr,1,1 ) } function _TBSetD() { =20 this.ChgState( gFaceClr,gFaceClr,0,0 ) this.mIsOn =3D 0 } function _TBSetE() { var t=3Dthis if( !t.GetState() ) t.ChgState( gFaceClr,gFaceClr,0,0 ) else t.ChgState( gShadowClr,gHiliteClr,1,1 ) t.mIsOn =3D 1 } function _TBP() { var t=3Dthis if( t.mIsOn ) {=20 if( t.UserAction !=3D null ) t.UserAction() if( !t.GetState ) return if( t.GetState() ) t.SetPressed() else t.SetActive() } =20 } function _TBUI( clr1,clr2,lOffset,tOffset ) { SetBorder( GetObj( this.mObjId ),clr1,clr2 ) Offset( GetObj( this.m_elementsId ),lOffset,tOffset ) } function Offset( obj, top, left ){ obj.style.top=3Dtop; obj.style.left=3Dle= ft } function SetBorder( obj, upperLeft, lowerRight ) { s=3Dobj.style; s.borderStyle =3D "solid" s.borderWidth =3D 1=20 s.borderLeftColor =3D s.borderTopColor =3D upperLeft s.borderBottomColor=3D s.borderRightColor =3D lowerRight } function GetBtnObj(){ return gBtnArr[window.event.srcElement.id] } function BtnOnOver(){ b=3DGetBtnObj(); if( b !=3D null ) b.SetActive() } function BtnOnDown(){ b=3DGetBtnObj(); if( b !=3D null ) b.SetPressed() } function BtnOnOut(){ b=3DGetBtnObj(); if( b !=3D null ) b.SetInactive() } function BtnOnUp() { b=3DGetBtnObj() if( b !=3D null ) b.Perform() else Upd() } function GetNtsState(){ return parent.gNtsOpen } function GetOtlState(){ return parent.gOtlOpen } function GetOtlTxtState(){ return parent.gOtlTxtExp } function NtsBtnSetFlag( fVal ) { s=3Ddocument.all.item( this.m_flagId ).style s.display=3D"none" if( fVal ) s.display=3D"" else s.display=3D"none" } function _BSetA_Border(){ b =3D gBtnArr[this.mObjId]; if( b !=3D null ) b.S= etActive() } function _BSetI_Border(){ b =3D gBtnArr[this.mObjId]; if( b !=3D null ) b.S= etInactive() } function _BSetP_Border(){ b =3D gBtnArr[this.mObjId]; if( b !=3D null ) b.S= etPressed() } function _BSetA_BorderImg() {=20 b =3D gBtnArr[this.mBorderId]=20 if( b !=3D null && this.mIsOn && !b.GetState() ) { obj=3Dthis.ChgState( gHiliteClr,gShadowClr,2 ) obj.style.posTop=3D0 } } function _BSetI_BorderImg() {=20 b =3D gBtnArr[this.mBorderId] if( b !=3D null && this.mIsOn && !b.GetState() ) { obj=3Dthis.ChgState( gFaceClr,gFaceClr,1 ) obj.style.posTop=3D0 } } var gHiliteClr=3D"THREEDHIGHLIGHT",gShadowClr=3D"THREEDSHADOW",gFaceClr=3D"= THREEDFACE" var gBtnArr =3D new Array() gBtnArr["nb_otl"] =3D new TxtBtn( "nb_otl","nb_otlElem",parent.ToggleOtlPan= e,GetOtlState ) gBtnArr["nb_otlElem"] =3D new TxtBtn( "nb_otl","nb_otlElem",parent.ToggleOt= lPane,GetOtlState ) gBtnArr["nb_nts"] =3D new ImgBtn( "nb_nts","nb_ntsBorder",10,parent.ToggleN= tsPane ) gBtnArr["nb_nts"].SetActive =3D _BSetA_BorderImg; gBtnArr["nb_nts"].SetInactive =3D _BSetI_BorderImg; gBtnArr["nb_ntsBorder"] =3D new TxtBtn( "nb_ntsBorder","nb_ntsElem",parent.= ToggleNtsPane,GetNtsState ) gBtnArr["nb_ntsElem"] =3D new TxtBtn( "nb_ntsBorder","nb_ntsElem",parent.To= ggleNtsPane,GetNtsState ) gBtnArr["nb_prevBorder"] =3D gBtnArr["nb_prev"]=3D new ImgBtn( "nb_prev","n= b_prevBorder",30,parent.GoToPrevSld ) gBtnArr["nb_nextBorder"] =3D gBtnArr["nb_next"]=3D new ImgBtn( "nb_next","n= b_nextBorder",30,parent.GoToNextSld ) gBtnArr["nb_sldshw"]=3D new ImgBtn( "nb_sldshw","nb_sldshwBorder",18,parent= .FullScreen ) gBtnArr["nb_sldshwBorder"] =3D new TxtBtn( "nb_sldshw","nb_sldshwBorder",pa= rent.FullScreen,null ) gBtnArr["nb_sldshwBorder"].SetActive =3D _BSetA_Border; gBtnArr["nb_sldshwBorder"].SetInactive =3D _BSetI_Border; gBtnArr["nb_sldshwText"] =3D new TxtBtn( "nb_sldshw","nb_sldshwText",parent= .FullScreen,null ) gBtnArr["nb_sldshwText"].SetActive =3D _BSetA_Border; gBtnArr["nb_sldshwText"].SetInactive =3D _BSetI_Border; gBtnArr["nb_voice"] =3D gBtnArr["nb_voiceBorder"] =3D new ImgBtn( "nb_voice= ","nb_voiceBorder",18,parent.ToggleVNarration ) gBtnArr["nb_otlTxtBorder"] =3D gBtnArr["nb_otlTxt"]=3D new ImgBtn( "nb_otlT= xt","nb_otlTxtBorder",23,parent.ToggleOtlText ) gBtnArr["nb_ntsBorder"].m_flagId=3D "nb_nts" gBtnArr["nb_ntsBorder"].SetFlag =3D NtsBtnSetFlag gBtnArr["nb_otlTxt"].ChangeIcon=3D GetOtlTxtState /********************************************* Context menu implementation _CM() is the function that's hooked up to the oncontextmenu event. Once we're asked to show the menu, we first build it by creating DIVs on-the-fly. Then we position it=20 within the screen area so it doesn't get clipped. Creating the DIVs using createElement() means we don't have to write out any extra HTML into the slide HTML files. **********************************************/ var sNext=3D"Next",sPrev=3D"Previous",sEnd=3D"End Show",sFont=3D"Arial",sAr= row=3D"Arrow",sFreeform=3D"Freeform",sRect=3D"Rectangle",sOval=3D"Oval" function ShowMenu() { BuildMenu(); var doc=3DPPTSld.document.body,x=3DPPTSld.event.clientX+doc.scrollLeft,y= =3DPPTSld.event.clientY+doc.scrollTop m =3D PPTSld.document.all.item("ctxtmenu") m.style.pixelLeft=3Dx if( (x+m.scrollWidth > doc.clientWidth)&&(x-m.scrollWidth > 0) ) m.style.pixelLeft=3Dx-m.scrollWidth m.style.pixelTop=3Dy if( (y+m.scrollHeight > doc.clientHeight)&&(y-m.scrollHeight > 0) ) m.style.pixelTop=3Dy-m.scrollHeight m.style.display=3D"" } function _CM() { if( !parent.IsFullScrMode() ) return; if(!PPTSld.event.ctrlKey) { ShowMenu() return false } else HideMenu() } function BuildMenu() { if( PPTSld.document.all.item("ctxtmenu") ) return var mObj=3DCreateItem( PPTSld.document.body ) mObj.id=3D"ctxtmenu" mObj.style.visibility=3D"hidden" var s=3DmObj.style s.position=3D"absolute" s.cursor=3D"default" s.width=3D"120px" SetCMBorder(mObj,"menu","black") var iObj=3DCreateItem( mObj ) SetCMBorder( iObj, "threedhighlight","threedshadow" ) iObj.style.padding=3D2 CreateMenuItem( iObj,sNext,M_GoNextSld,M_True ) CreateMenuItem( iObj,sPrev,M_GoPrevSld,M_HasPrevSld ) =09 CreateSeparator( iObj ) CreateMenuItem( iObj,sEnd,M_End,M_True ) mObj.style.visibility=3D"visible" } function Cancel() { window.event.cancelBubble=3Dtrue; window.event.returnVa= lue=3Dfalse } function Highlight() { ChangeClr("activecaption","threedhighlight") } function Deselect() { ChangeClr("threedface","menutext") } function Perform() { e=3DPPTSld.event.srcElement if( e.type=3D=3D"menuitem" && e.IsActive() ) e.Action() else PPTSld.event.cancelBubble=3Dtrue } function ChangeClr( bg,clr ) { e=3DPPTSld.event.srcElement if( e.type=3D=3D"menuitem" && e.IsActive() ) { e.style.backgroundColor=3Dbg e.style.color=3Dclr } } function M_HasPrevSld() { return( parent.HasPrevSld() ) } function M_GoNextSld() { if( gIsEndShow ) M_End(); else GoToNextSld() } function M_GoPrevSld() { if( gIsEndShow ) { gIsEndShow=3D0; history.back();= PPTSld.event.cancelBubble=3Dtrue; } else GoToPrevSld() } function M_True() { return true } function M_End() { window.close( self ) } function CreateMenuItem( node,text,action,eval ) { var e=3DCreateItem( node ) e.type=3D"menuitem" e.Action=3Daction e.IsActive=3Deval e.innerHTML=3Dtext if( !e.IsActive() ) e.style.color=3D"threedshadow" e.onclick=3DPerform e.onmouseover=3DHighlight e.onmouseout=3DDeselect s=3De.style; s.fontFamily=3DsFont s.fontSize=3D"9pt" s.paddingLeft=3D2 } function CreateSeparator( node ) { var sObj=3DCreateItem( node ) SetCMBorder(sObj,"menu","menu") var s=3DsObj.style s.borderTopColor=3D"threedshadow" s.borderBottomColor=3D"threedhighlight" s.height=3D1 s.fontSize=3D"0px" } function CreateItem( node ) { var elem=3DPPTSld.document.createElement("DIV") node.insertBefore( elem ) return elem } function SetCMBorder( o,ltClr,rbClr ) { var s=3Do.style s.backgroundColor=3D"menu" s.borderStyle=3D"solid" s.borderWidth=3D1 s.borderColor=3DltClr+" "+rbClr+" "+rbClr+" "+ltClr } ------=_NextPart_01C8328C.B490AE10 Content-Location: file:///C:/2D693CD7/CoreLesson7_files/fullscreen.htm Content-Transfer-Encoding: quoted-printable Content-Type: text/html; charset="us-ascii" ------=_NextPart_01C8328C.B490AE10 Content-Location: file:///C:/2D693CD7/CoreLesson7_files/notes_flag.gif Content-Transfer-Encoding: base64 Content-Type: image/gif R0lGODlhCgAKAPcAAAAAAIAAAACAAICAAAAAgIAAgACAgICAgMwENMTExPz8/AAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAMDAwP8AAAD/AP//AAAA//8A/wD//////ywAAAAACgAKAEAIKgDx4UNA sKDAgQUTJiCogGHDhBAfFlRAMSFCiAguTozYUGJEiAk0EhQYEAA7 ------=_NextPart_01C8328C.B490AE10 Content-Location: file:///C:/2D693CD7/CoreLesson7_files/buttons.gif Content-Transfer-Encoding: base64 Content-Type: image/gif R0lGODlhWAESAPf4AAAAAIAAAACAAICAAAAAgIAAgACAgICAgAQEBISEBASEBISEhAQEhMTExAQE /KTM9Pz8/ERERPz8BAT8/KSkpGRkhMTcxCRkxAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA AAAAAAAAAAAAAAAAAAAAAMDAwP8AAAD/AP//AAAA//8A/wD//////yH5BAEAAPgALAAAAABYARIA QAj/APEJHEiwoMGDCBMqXMiwocOHECNKnEixosWLGCEiQKCRo8YDIEHig2DxAD4LKD1avDDhgUuV GUOGbHBR5QGYFBG4fHAB58EKECJEwCfUYAWPFGAygLCRKQIIUKM6WAohKUGgCikcFWh1INWoYKVS 7SrQ41GbIhGYLAuVQVOoC+IyXUuUAkG1HE3KFDhAwkgJc5/qDZmxsOHDiBMrXsy4sePDGyP7lChT 5MULmDPnlDw5YmW6FTNrfgi0aNGEZPEtbfo2bNTUpYeeRph69dPWrqvCNFuBIGG1A59CYPAVQtwF cw0OxWdTIOiBCQAjaAB17fOFII8voGmRc+eOkilm/z9OvTtnjN4hYk1YoT3H2rnBOphPAB9skgq3 2lcaX/5YnJVt9BloAar12UEIRGCZdQghMABI1Tn32IQUVthYexhmqGGGMBHAgIfEhSiiiATAtOGJ GnYI4ogsEldicAYOGNJGZaml3Y0L3NTZUBz1xlB0PUoUI0jlVWRSVN89xBKSGB1YU1TMoRfVBEle hR9HQs1GEHxQ3RZZbveZthxt/LEmXHyp5XWABSCpaRJwbM13gAACPHVccgJFgF+NEhqUAEkQSCfc ddhVhh5dVTaEAEsTUNlkZUWKN9BNGDE6QU8OrSdbllzpxyVTTrU21Uj3scfhp7nNpyoDaTIEJ3P9 If8J2kbLNYegg9JRBwGhFvbq66+ZUiDssMQWK2yHxiZLrInKNotss8l+B5yBrr5p2UIJvortANoC 6+234IbLla/elRtZjeamh5CC3Sb0YLvixivvYkDFGlZqBNh7r4n6goVvv6/ZlCicN+kL71ALTnpQ dCIZp7CihkLA3UQmoWRBogyxtBPGCTnZncVR1rSTo5nuydC/Eo8kUH+lOoTyyvjoCuZu+PjYIKLD rZybtrM1d10C0QXKEVz48GrQkEeWdFJKlbb0UmEeV0SzyC6RvNB646LWIVjUNeC1zAFb+RDKXksM 9r531bwmpQW9+hQDDsx5pqwDRWBXcFES2hc+gEn/wJGdEEWdE6LoWcoxQweaTNmkhydkKaYMYY2Q p1unbLl/pPKbn3v7EZRvrKvqlja2ONvrtoIw9tn2g32/tQBlhtYkU+MNikZ7QYlPDPuMldpOmuJX nVo5VF3HjI+q89mteX5IDd/fVFClma5kiE4f2XUJhlz09gj2NbTDRifkmu7zXjR++RVJ/lPznuvr QH2iD6S+UewP9Dnon6d2NLwN8n90BB6hC68cFMCHoe+ACASP9c4DowUyEF0OPFcDI0ij/VXPaAKC UfhS95AKGoQ7IBRICI1HwhGaUIQoLGEKT6jCFrLwhSuMoQtlCMMZ2rCGOKShDm+4wxzy8Ic+DGIP B4cIRCKGMCAAOy== ------=_NextPart_01C8328C.B490AE10 Content-Location: file:///C:/2D693CD7/CoreLesson7_files/frame.htm Content-Transfer-Encoding: quoted-printable Content-Type: text/html; 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	Gen= eral lesson description
	This l= ecture continues developing the general objective of the previous one. It offers explanations on analytic study designs including case-control studies, co= hort studies, and randomized controlled trials.
	It exp= lains these designs by means of examples from the literature and explores potential u= ses, advantages and disadvantages of each methodology.


	Analyt= ical studies are designed to test one or more hypotheses. These studies usually focus = on an exposure (which frequently is a risk or protective factor for injuries= ), and its relation to a specific outcome or set of outcomes (injuries).
	They c= an be used to evaluate treatments or prognosis as well as programmes and policies. These studies do not focus necessarily on injured people but can evaluate the effect of environmental modifications, implementation of laws or the establishment of community programmes.
	They c= an be divided into two types of research designs: observational and intervention.
	Obs= ervational studies include several research designs such as case-control studies, cohort studies, cross-sectional studies, and longitudinal designs.=
	Int= ervention or experimental studies include randomized controlled trials (RCTs) and quasi-experimental studies.
	The ma= in difference between an observational and an intervention study is that in the latter,= the researcher has control over the exposure or treatment status of the study subjects. This is useful to improve the validity of the comparisons made = in the study (1).


	The cross-sectional study examines the relationships between injuries (outcomes), and oth= er relevant variables (exposures or risk factors), as they exist in a defined population, at one particular point in time.
	Althou= gh the cross-sectional study may reveal useful associations, because each subject’s status on both outcome and risk factor is determined at t= he same time, no causal inferences can be obtained from this design. Such an analysis can only suggest hypotheses regarding risk or protective factors= and is therefore rarely used for testing a cause-effect hypothesis.


	The st= udy described in the slide investigated risk factors for non-fatal injury among rural children, aged 0–17 years, in Iowa, in the United States, using a cross-sectional survey (2).= The main risk factors associated with injury in this sample were age, members= hip of a sporting team, binge drinking and sedative use. Girls who binge dran= k or participated in team sports were more likely to be injured than boys who = did the same.
	Object= ive
	To ide= ntify risk factors for non-fatal injury among rural children.
	Design=
	Cross-= sectional health interview survey, 1994-98.
	Settin= g
	A rura= l Iowa county, not adjacent to a metropolitan area.
	Subjec= ts
	Strati= fied, random sample of households, including all resident children and adults.<= br>
	Main o= utcome measures
	Injury= episodes in the past 12 months among children aged 0–17 years and the parental = and child characteristics associated with these episodes.
	Result= s
	Of the= 621 children in participating households, 137 or 22.1% were injured during the past 12 months. Children aged 5–17 in a sports team were 1.88 times (95% confidence interval (CI) 1.07–3.31) more likely than other children= to be injured. Children aged 12–17 who binge drink were 3.50 times (95= % CI 1.31–9.50) more likely than other children to be injured. Compared = with children not in sports teams, girls in teams were 2.26 times (95% CI 1.02–5.13) more likely while boys in teams were 1.60 times (95% CI 0.71–3.68) more likely to have an injury episode. Compared with children who did not binge drink, girls binge drinking were 8.11 times (9= 5% CI 1.52–43.33) more likely while boys binge drinking were 2.19 time= s (95% CI 0.70–6.84) more likely to have an injury episode.
	Conclu= sion
	Local = studies such as this can provide useful clues regarding the etiology of injury. Some k= nown and some new potential risk factors including behavioural aspects for childhood non-fatal injury in a very rural area were investigated. It is planned to address these cross-sectional findings in future longitudinal follow up of this population.


	The ma= in advantage of this design is that it can reveal useful associations, as in the examp= le on the previous slide, where an association was found between certain you= th behaviours such as binge drinking and the risk of injury.
	As men= tioned before, the main disadvantage is that it is impossible to make inferences about causality based on temporal associations.


	A case= -control study appears to approach testing a causal hypothesis backwards by proceeding f= rom effect to cause (see slide). The researcher begins by identifying persons= who have sustained an adverse outcome of interest (e.g. an injury) – the cases, and persons who did not experience the adverse outcome – the controls. The next stage is to gather information about the past exposure= of each group to the risk factor or factors of interest. Only exposure that preceded the outcome in cases (or a comparable “reference period= 221; in controls) is considered.
	The re= sulting data can be analysed to estimate the strength and statistical significance of = the association between exposure and outcome. A case-control study may be eit= her retrospective or prospective in that the cases in a case-control study may have already experienced the outcome of interest when the study begins (retrospective), or they may be new cases that occur as the study proceeds (prospective) (1).
	As men= tioned above, in a case-control study, a case may be an injured person and the control could be a person not injured. A case could also be a section of road whe= re a vehicle hit a tree and the control could be sections of road that the veh= icle traversed without hitting trees.
	The re= search question here is how individual or environmental risk factors differ betw= een the cases and the controls.
	This d= esign is often used for rare outcomes, such as injury, as it is very efficient. Cases and controls are selected and associations are established based upon potenti= al differences in exposures to one or more factors.


	This e= xample of a case-control study was conducted in Lima, Peru by Delgado and colleagues = (3) to determine the risk factors associated with burns in children aged less than 18 years.
	Cases = were defined as children who came to hospital with a burn injury. One control matched = for age and sex was selected for each case, from patients with other conditio= ns who presented at the same hospital.
	A ques= tionnaire was administered to all consenting guardians of children admitted to the burns (cases) and general medicine (controls) units during a period of 14 month= s. Guardians of patients were questioned regarding etiology of the injury, demographic and socioeconomic data.
	A tota= l of 740 cases and controls were enrolled. Altogether 77.5% of the cases burns occurred = in the patient's home, with 67.8% in the kitchen; 74% were due to scalding. = Most involved children younger than 5 years. Lack of water supply (odds ratio = (OR) 5.2, 95% confidence interval (CI) 2.1–12.3), low income (OR 2.8, 95= % CI 2.0–3.9), and crowding (OR 2.5, 95% CI 1.7–3.6) were associat= ed with an increased risk. The presence of a living room (OR 0.6, 95% CI 0.4–0.8) and better maternal education (OR 0.6, 95% CI 0.5–0.= 9) were protective factors.
	It was= concluded that to prevent burns, interventions should be directed to low socioecono= mic status groups and these interventions should be designed according to loc= al risk factors.


	The ma= in advantage of a case-control study is that it is good for rare outcomes and ideal for studying multiple risk factors that preceded the injury outcome as seen in the previous example.
	The ma= in disadvantage of a case-control study is that it cannot yield information = on absolute risk but only on relative risks of injury.


	The ke= y elements that define a cohort study are the designation of a population in which exposure status is known, then a period of time elapses, and one or more outcomes are observed or measured.
	In a c= lassical cohort study, there are two cohorts: one exposed to the risk factor or factors under consideration and the other unexposed. The comparison focus= es on the measurement of good and bad outcomes related to the exposure.
	These = studies can be prospective, meaning that at the beginning of the study no outcomes of interest (e.g. injuries) have occurred or retrospective, in which case exposures and events might have occurred but the researcher assembles the= two cohorts historically and follows them from the past towards the present.<= /font>
	The di= agram above outlines the classical cohort study comparisons.
	In the= field of injury epidemiology and prevention research, a cohort study may require injury as a criterion for membership of the cohort. Individuals are usual= ly identified from a medical facility and followed for outcomes of interest (e.g. disability). While these studies are essentially studies of prognos= is, they do not differ in principle from cohort studies of the cause of injury (4).
	In all= observational studies an important issue to consider is the issue of confounding. Confounding relates to whether or not there are systematic differences between persons exposed versus those not exposed to a risk factor of interest. These systematic differences may be the source of the observed differences in outcome rather than exposure to the factor of interest.


	The ex= ample shown here compares two groups of women within a population: those exposed to intimate partner violence and those not exposed (5).
	In this retrospective cohort study, female residents of King County, Washington, = who had filed a civil protection order in 1992 were considered exposed to intimate partner violence. A comparison group consisted of women of the s= ame age who had not filed protection orders.
	The ou= tcomes of interest in this case were overall and diagnosis-specific hospital admiss= ion rates and the relative risk of hospitalization associated with abuse in t= he 12-month period prior to seeking protection orders.
	Object= ives
	This s= tudy assessed the history of hospitalization among women involved in violent intimate relationships.
	Method= s
	In thi= s one-year retrospective cohort study, female residents of King County, Washington, = who were aged 18–44 years and who had filed for a protection order were compared with non-abused women in the same age group. Outcome measures included overall and diagnosis-specific hospital admission rates and rela= tive risk of hospitalization associated with abuse.
	Result= s
	Women = known to be exposed to a violent intimate relationship were significantly more likely= to be hospitalized with any diagnosis (age-specific relative risks (RRs) ran= ging from 1.2 to 2.1), psychiatric diagnoses (RR =3D 3.6, 95% confidence inter= val (CI) 2.8–4.6), injury and poisoning diagnoses (RR 1.8, 95% CI 1.2–2.8), digestive system diseases (RR 1.9, 95% CI 1.3–2.9),= and diagnoses of assault (RR 4.9, 95% CI 1.1–22.1) or attempted suicide= (RR 3.7, 95% CI 1.6–9.2) in the year before filing a protection order.<= /font>
	Conclu= sion
	This s= tudy showed an increased relative risk of both overall and diagnosis-specific hospitalizations among abused women. Intimate partner violence has a significant impact on women's health and use of health care.


	A p= rospective cohort study is useful when applied to injury problems that are common or that require a short follow-up, and can be useful in evaluating the effectiven= ess of an intervention. A prospective cohort study can, however, be very expensive if studying an uncommon outcome or if the follow-up period requ= ired to measure its incidence is long.
	The co= hort study design is also useful for studying rare exposures, such as an unusual occupation or activity, as all available exposed individuals can form one cohort and a sample of the many unexposed individuals can form a comparis= on cohort.
	Cohort= studies can also yield information about absolute level of risk (i.e. incidence estimates) for exposed and unexposed persons.
	Ret= rospective cohort designs are also useful for studying outcomes that are relatively = rare where pre-existing information is available on large populations (e.g. Medicaid enrolees in the United States). In general, however, the feasibi= lity of a retrospective cohort study depends heavily on the availability of historical data (with details of the subjects’ exposure status at s= ome time in the past) and on having comparable follow-up data on exposed and unexposed subjects (1).


	Longit= udinal studies incorporate repeated measurements of an outcome at the individual or group level over time. Changes in outcome are then evaluated in relation to kno= wn changes in one or several exposures.
	The si= mplest design related to this is a before-after study that compares the frequency of an outcome (injury) in a group on two occasions: before and after the occurr= ence of a certain exposure. This exposure can be the passage of a law or the occurrence of an environmental change.
	In the= hypothetical example above, a measurement of outcome (the rate of injury) is taken bef= ore and after an intervention is put in place. The graph suggests that there = has been a fall in injury rates since the intervention. However, a limitation= of the before-after design is that any differences observed may just represe= nt the continuation of an existing trend that was unrelated to the intervent= ion.


	Some p= rotection against the possible misinterpretation of the results of a before-after s= tudy is offered by the interrupted time-series design. This involves taking several measures of the outcome frequency over time, both before and afte= r a new programme or policy is initiated. By taking multiple measures over ti= me, pre-existing trends can become apparent.
	In the= example above, the presence of multiple measures of the injury rate over time mak= e it clear that the injury rate was actually increasing before the implementat= ion of the intervention, and that it began to decrease after the intervention. Based solely on the information in the before-after study (see previous slide), one could not be sure that the rate of injury was not already declining before the implementation of the intervention.


	As men= tioned earlier, using multiple measurements of outcome over time can control for pre-existing secular changes.
	Anothe= r advantage of these studies is that they can evaluate the effects of widely applied interventions (such as laws) and are usually low-cost if the data is alre= ady available from existing sources.
	Before= -after studies may be subject to confounding from pre-existing secular trends and the results should therefore be treated with caution.


	The ty= pe of intervention study that does not involve random designation of subjects to comparison groups is termed a quasi-experiment. This is in contrast to the randomized controlled trial that is known as a true experiment.
	This k= ind of study is usually conducted in the situation where a randomized controlled trial= is not possible. Assignment of the either the treatment (intervention) or control (comparison) group is non-random.
	Althou= gh a quasi-experiment is an intervention study, it is more like an observation= al study than a randomized controlled trial in one important way. One cannot depend on the intervention and control groups being similar with regards = to other determinants of outcome. Therefore, attempts should always be made = to ensure that the intervention and control groups are as alike as possible = on certain key characteristics to avoid confounding.


	A quas= i-experiment is often employed to evaluate the effect of a programme, policy or regula= tion at the population level. Given that a law, for example, is enacted, the simplest question is whether it reduces injuries?
	As we = have seen the simplest, but sometimes misleading, research design used to answer this question is to compare injury rates before and after the law is enacted. = If other factors are changing that would have increased or decreased injuries during the same period, the change in injury rate could be falsely attrib= uted to the law.
	Robert= son (6) cites the example of the situation in the city of Chicago, in the United States, during the period 1970–71, when a supervising judge mandated a seven-day jail sentence for drunk driving. During this period the death r= ate declined and the rule was declared a success.
	Aware = of the threats to validity in before-after comparisons, researchers designed a quasi-experimental study to examine the effects of Chicago’s judici= al policy. Comparisons of the death rates in Chicago and the nearby city of Milwaukee (which did not have a policy of mandatory jail sentences), duri= ng the same period, showed that a similar decline occurred at the same time = in Milwaukee. The reduced death rates were likely the result of recession in= the economy or changes in weather patterns that happened to occur at the same time as the judge’s sentencing policy.


	The ra= ndomized controlled trial (RCT), which allocates individuals randomly to a treatme= nt (intervention) versus non-treatment (control or comparison) group, is the strongest type of design in the sense that it is the most effective in controlling for confounding. Random assignment of subjects to different treatment groups tends, on average, to balance the groups on other factors that could influence the outcome. It is , therefore, the best study design for actually obtaining a quantitative estimate of a causal association between an exposure or treatment and an outcome.
	A simp= le two-group randomized design is shown above. Subjects are randomly assigned to one of two groups, here the treatment (or intervention) group and the control (or comparison) group. Often one treatment is experimental while the other ma= y be no treatment, a specific alternative treatment or usual care. Both groups= are then followed prospectively and the incidence of good and bad outcomes is measured and compared.
	As the= design of choice among intervention studies, the RCT should be the first study desi= gn option considered for treatment and programme evaluations, resorting to o= ther less rigorous designs only if there are major obstacles to the RCT (1).


	This e= xample evaluates the effect of a violence prevention curriculum in the preventio= n of aggressive behaviours. Random allocation does not have to be exclusively = for individuals. In this case, schools were randomly allocated to receive or = not a violence prevention curriculum (7).
	Object= ive
	To det= ermine if a commonly used violence prevention curriculum, Second Step: A Violence Prevention Curriculum, leads to a reduction in aggressive behaviour and an increase in pro-social behaviour among elementary school students.=
	Design=
	Random= ized controlled trial.
	Settin= g
	Urban = and suburban elementary schools in the state of Washington.
	Partic= ipants
	Six ma= tched pairs of schools with 790 second-grade and third-grade students. The students were= 53% male and 79% white.
	Interv= ention
	The cu= rriculum uses 30 specific lessons to teach social skills related to anger management, impulse control and empathy.
	Main o= utcome measures
	Aggres= sive and pro-social behaviour changes were measured two weeks and six months after participation in the curriculum by parent and teacher reports (Achenbach Child Behavior Checklist and Teacher Report Form, the School Social Behav= ior Scale, and the Parent-Child Rating Scale), and by observation of a random sub-sample of 588 students in the classroom and playground or cafeteria settings.
	Result= s
	After = adjusting for sex, age, socioeconomic status, race, academic performance, household size and class size, the change in scores did not differ significantly between= the intervention and control schools for any of the parent-reported or teacher-reported behaviour scales. However, the behavioural observations = did reveal an overall decrease two weeks after the curriculum in physical aggression (P =3D 0.03) and an increase in neutral or pro-social behaviour (P =3D 0.04) in the intervention group compared with the control group. Most effects persisted six months later.
	Conclu= sion
	The Se= cond Step violence prevention curriculum appears to lead to a moderate observed decrease in physically aggressive beha= viour and an increase in neutral and pro-social behaviour in school.


	The RC= T is considered the “gold standard” of research design as it is mo= re likely than other designs to establish causal associations and is less li= kely to suffer from confounding and bias.
	As wit= h prospective cohort studies and quasi-experiments, RCTs may be too expensive or impractical if the primary outcome of interest is rare, or if long period= s of follow-up are required before any intervention effects are apparent. Randomization may also be politically or morally unacceptable to collaborating organizations or individuals (random assignment of any protective device would raise serious ethical questions).


	There = are different methodologies for summarizing research. They range from a state-of-the-art review of a subject to systematic reviews that define certain parameters = for inclusion or exclusion of studies in order to facilitate comparability.
	There = are more elaborate analyses such as the meta-analysis, which synthesizes the resul= ts of several studies that used the same methodology into one overall estima= te of association between exposures and outcomes.
	These = methods are extremely useful as precursors to studies involving primary data collecti= on, as one should always have a firm grasp of the current state of knowledge about a specific injury subject, to be clear where the gaps are, before embarking on a new study.


	Resear= ch should be aimed at responding to important social problems of concern to the commun= ity, and should contribute to the identification of best practice through the evaluation of treatments, programmes or policies.
	To sum= marize, the first step in any research project is to ask a question or state a hypothesis. To find out what needs to be known, one must first find out w= hat is already known by reviewing the literature.
	The ch= oice of research study design will then depend on the question being asked. Some research simply attempts to describe the current state of affairs, without any expectation about what might be found. For example, what are the most common injuries associated with motorcycle crashes? How common are burns = and scalds among preschool children? This kind of research is typically best addressed by a descriptive study (1). The type of descriptive study chosen will depend on the nature of the question and the nature of the data available.
	In con= trast, other studies seek to test a specific hypothesis. Often the research question f= or an analytical study is whether a certain cause (which may be an intervent= ion) leads to a certain effect. For example, does a programme to prevent falls= in the elderly significantly reduce the incidence of falls? Do bicycle helme= ts protect wearers against head injury in the event of an accident? These ki= nds of questions are usually best addressed by an analytical study design (1). The type of analytical study design chosen will again depend on the natur= e of the question, the potential to manipulate exposure or treatment by the investigator, the frequency of the outcome of interest and opportunities = or barriers (e.g. resources availability) that may exist locally.