Types of Epidemiological Studies | Essay | Epidemiology | Medical Science

Read this essay to learn about the two main types of epidemiological studies. The types are:- 1. Observational Epidemiological Studies 2. Experimental Epidemiological Studies. 

Essay # 1. Observational Epidemiological Studies:

(a) Descriptive Studies

(b) Analytical Studies

(i) Case control—Case Reference

(ii) Cohort—Follow-Up.

(a) Descriptive Studies:

Descriptive epidemiology deals with the study of the magnitude of a disease or condition and its distribution or the magnitude of exposure to risk factors and other distribution within a human population with reference to person, place and time of occurrence.

In order to do this, the descriptive studies have to deal with:

(I) Description of the occurrence of a disease or condition or the exposure to risk factors:

1. What is a ‘case’ or what is a risk factor and what is exposure?

2. Who are the persons affected and how?

3. What is (are) the place(s) of occurrence of case or exposure?

4. What is the time of occurrence of case or exposure?

The points to be kept in mind in answering the above questions are:

1. ‘Case’ and ‘exposure’ must be defined in objective measurable terms.

2. Adequate relevant details about persons, namely Age, Sex, Marital Status, Occupation, Education, Socio-economic Status and others like Family size, Parity, Birth order, Maternal age, etc., as appropriate for the study should be collected.

3. Details on the place of occurrence (including details on migration), like urban/rural, regions within a Country or State, etc. needed.

4. The time interval or measurement of occurrence of cases or exposure should be clearly specified. Seasonal changes should be taken of occurrence of disease or exposure can be influenced by natural catastrophies, etc.

(II) Purpose of Descriptive Studies:

1. Estimate the prevalence or incidence of a disease or condition in a defined population group.

2. Describe the characteristics of people, with the disease or condition at a point in time or over a period of time.

3. Estimate the frequency and duration of exposure to risk of people.

4. Describe the characteristics of ‘exposed’ people at a point of time or over a period of time.

Descriptive studies can, therefore, be either cross-sectional (that is, data collected from a cross-section of the population at a point to time) or longitudinal (data collected at a number of chosen points of time) or can be in the nature of Surveillance Studies or continuous monitoring studies.

The results of such studies generally serve one or two purposes :

(a) To develop hypothesis to be tested subsequently through specially designed studies and

(b) To develop strategies for reducing or preventing exposure to strongly suspected risk factors.

Special surveys, including physical examina­tions, anthropometric measurements, etc., reveiw of records (provided they are complete and accurate) from specific groups (industrial labour, government servants, armed forces, etc.), vital statistics, etc. are the sources of data for Descriptive studies.

(b) Analytical Studies:

(i) Case-Control Studies:

The study of Causation and of prevention and Control of diseases or health problems can be looked upon as a four-stage process.Case-Control studies and Cohort Studies form the first two stages of this process and Experimental Studies and Practical Prevention or Control Programmes forms the third and fourth steps.It will be altered in some situations,it may not be possible or desirable to carry out Cohort Studies or Experimental Studies.

In the Case-control study, we proceed from an observed ‘effect’ (a disease or health condition) to identify possible causal factors. The nucleus of the study, therefore, is a series of cases of a disease or condition on whom information is obtained to find out the frequency of previous exposure to a suspected cause.

This is compared with the frequency of occurrence of the suspected cause in one or more groups of persons who do not have this condition or disease. In other words, the case-control study is a comparative study between a group of cases and one or more groups of ‘controls’.

It may, at this point, be helpful to look briefly at an example to understand the sequence of epidemiological research. A current problem of interest related to the role of dietary factors in disease is that of the relationship between dietary factors and Colorectal Cancer.

The epidemiological evidence that has accrued on this problem can be described as indicated below:

1. Identification of the problem

2. Identification of the potential role of diet as a risk factor

3. Testing the hypothesis of ‘on the role of diet as a risk factor’

4. Seek evidence to strengthen the hypothesis on the role of diet

5. Test the evidence of bile acids through an experimental study

6. Practical prevention trials

Descriptive Study of age and sex specific Colon cancer death rates in a population.

Comparative study of age and sex specific colon Cancer death rates in a predominantly meat eating population versus a predominantly vegetarian population.

Comparative study of Colon Cancer death rates in the meat eating and non-meat eating subgroups of populations within the predominantly meat eating population (case-control study).

Faecal analysis reveals higher concentrations of faecal bile acids in Colon Cancer cases than in Controls.

Experimental demonstration obtained that dietary manipulation in humans alters faecal bile acids.

In free-lining population, altered dietary in-take results in reduced incidence of Colon Cancer.

Since the Case-control study looks from ‘effect’ to ‘possible cause’, it is also often called a ‘Retrospective study’.

Need of Controls:

The need for a Control group will become obvious if we remind ourselves of the fact that any given cause (or group of causes) may neither be necessary nor sufficient for the causation of a disease. Not all meat-eaters develop Colon Cancer and some vegetarians also develop Colon Cancer.

Because of this lack of one to one correspondence between cause and effect in either direction, evidence on association between diseases and ‘causal factors’ can be obtained only by comparing the relative frequency of occurrence of the ‘causal factors’ in cases and controls.

Section of Cases:

Having defined a ‘Case’ unambiguously using a set of reproduce-table criteria, careful attention should be paid to the source from which cases will be recruited.

These are, broadly speaking two sources:

(1) Case records from a hospital or hospitals, and

(2) Patients having the disease in a specified period of time.

The use of case records as source material for retrospective studies can suffer one or more of three drawbacks:

a. First, the case records may often be incomplete.

b. Secondly, there may be lack of uniformity in the recording to information for different patients, more detailed information being recorded for, say, cases with complications or multiple conditions.

c. Thirdly, a serious drawback of routine case records from hospitals is that they contain information only about factors that the clinician thinks are associated with the disease in question, they may merely reflect preexisting ideas about etiology.

The method of choice, therefore, is to select a sample of patients (ideally all patients suffering from the disease) from the population at a point or during a period of time. Use of hospital as the source of cases. But may be more convenient, may give rise to ‘selection bias’.

For example, not all cases may report to hospitals, resulting in some sort of self-selection affecting the representativeness of the suspected etiological factors themselves are associated with chances of admission to the hospital, selecting cases from the hospital can give rise to a spurious association.

Nevertheless, if a case-control study is designed to explore a series of hypothesis rather than test definitive hypothesis about a small number of factors—one may consider selection of cases from a hospital.

One further point of importance to note in the selection of ‘Cases’ is that it is advisable to use only newly diagnosed cases rather than previously diagnosed cases (or a ‘prevalence’ sample, as it is called).

The ‘prevalence’ sample excludes those that have died due to the disease and may, therefore, lead to a misinterpretation of factors conducive to long survival of patients as factors associated with excess liability to the disease.

Consider the following purely hypothe­tical illustration:

Assume that risk from all disease except disease X can be eliminated. Now consider a person at time ‘T’ being alive and free from disease X.

At a subsequent time ‘T’ this person can be in one of the following three states:

1. Alive without disease X

2. Alive with disease X

3. Dead from disease X

Now, suppose, we consider ‘factor Y’ as a potential etiological factor.

We can choose proba­bilities of contracting disease X and dying from it as shown below in the table:

A case-control study that used ‘prevalence’ sample at time T would exclude the ‘dead’ cases and incorrectly draw the inference that factor Y was an etiological factor while, in truth (in the hypothetical situation), Y is beneficial to X.

Even when “newly diagnosed” (instead of ‘prevalence’ cases) are included for study, care should be taken to see that in cases where the disease or condition had existed for some period before the diagnosis, factors associated with the course of illness are not identified as etiological factors. In other words, care should be taken to get information on the existence of the etiological factors in such cases before the disease started in them.

A further point for consideration is the possibility of selecting ‘cases’ on the basis of preliminary (or admission) diagnosis. They can help in identifying ‘interviewer bias’ by comparing information on ‘ultimately confirmed cases’ and ‘initially incorrectly diagnosed’ cases.

A final point of interest to note is that if the case fatality of a disease showed a strong differential between those who possessed the possible etiological factor under investigation and those who did not and, if the disease was rapidly fatal, a case-control study is not advisable. A ‘Cohort Study’ is advisable in such a situation.

Selection of Controls:

The function of a control group in a case-control study is to provide an estimate of the ‘expected’ exposure in the case group. It is, therefore, essential that the Control group be comparable with the Case group in all relevant respects except that the Controls do not suffer from the disease being studied.

Ideally, for a Case-control study, all cases of a disease occurring in a defined geographic area should form the Case group and a random sample of the general population should form the Control group. The point is that the Control group should be free of selection bias.

For example, if you are doing a Case-control study on aspirin use and myocardial infarction, you cannot use a set of arthritis patients as your controls or a set of peptic ulcer patients as the controls since neither of them would be representative of the general population with reference to use of aspirin.

On occasions, one may not be able to define the ‘universe’, for example, if case are to be picked from a hospital or hospitals, the ‘universe’ is not well-defined. In such a situation, choose cases and controls from the same source. Hospital controls usually are less affected by information bias than general population controls.

The question of matching—frequency match­ing or individual matching, also should be considered carefully in selecting a Control group. Matching is done for controlling potentially con­founding variables. (Effects of matched variables can, therefore, be not evaluated). When the controls are so selected that they have the same proportionate distribution of the matching variables as the case group, it is called ‘frequency matching’.

On the other hand, if an individual case is matched for one or more variables with an individual (or more than one) control, we have ‘paired’ matching. Matching on too many factors is neither feasible nor desirable. Lack of matching can be taken care of at the analysis stage through either stratification or by applying the analysis of covariance technique.

Statistical Assessment of Association:

The statistical significance of association is tested by using an appropriate X² test. (In individually matched cases and controls, McNemar’s X² is used instead of the usual X² test).

The strength of the association is measured where applicable, using a measure of ‘Relative Risk’ (RR). The relative risk is defined as the ratio of the incidence in the Case group to the incidence in the Control Group 1 Case/1 control.

However the case-control study, since it starts with an observed effect and not the suspected Cause, cannot get a direct estimate of ‘Incidence’ and cannot get a direct estimate of relative risk. An estimate of the relative risk can be calculated from the Case- control study by working out what is called the ‘Odds-Ratio’ (OR).

The table below shows the computation of the Odds Ratio:

An estimate of relative risk is given by the ratio:

a × d/b × c

This estimate is a reasonably good approximation to the ‘relative risk’ if the incidence of the disease is relatively low (about less than 5%).

Advantages of Case-Control Studies:

(1) Useful in health problems of low incidence.

(2) Useful in health problems with long latent interval.

(3) The study period is usually short and sampling is convenient making the study less expensive in time and resources.

(4) Can examine simultaneously a number of different hypotheses.

Disadvantages of Case-Control Studies:

(1) Considerable potential for selection bias exists.

(2) Information bias could occur since data are collected by recall after the occurrence of the disease. Also, if records are used, they could be incomplete.

(3) Cannot examine all possible outcomes of health exposure since ‘outcome’ is the starting point for the study.

(4) Cannot provide direct estimate of incidence or relative risk.

(ii) Cohort Studies:

Selection of Study Cohorts:

The comparison groups in Cohort studies are selected according to ‘Exposure’ (Exposed vs. Non-Exposed Groups) and the groups are followed in identical fashion to observe the development of a health problem over a defined period of time.

Selection of groups of individuals for Cohort Studies may arise in a variety of ways.

They may arise as:

(1) Groups that have experienced some special exposure, the results of which are to be evaluated,

(2) Groups that offer advantages for following-up because of special facilities or groups that facilitate identification of particular outcomes among its members and

(3) A combination of both the above reasons.

Occupational groups with heavy exposure to chemicals like workers in dye-stuff industry who we know now-run a high risk of urinary bladder cancer-groups or individuals exposed to heavy ionizing radiation during war, patients exposed to ionizing radiation are examples of special exposure groups.

Studies on survivors of atomic bombing of Hiroshima and Nagasaki are a particular example of a fruitful Cohort study of special exposure group. Persons enrolled in health insurance schemes. Obstetric populations, Army populations are all examples of groups that are easy to be followed up or that offer special facilities for identification of outcomes.

Exposure Data — Sources of Information:

There are three sources of information for exposure data:

(1) Records

(2) Information collected from individuals in the group.

(3) Information by medical examination or other special investigation.

It may be necessary, in a given study, to use information from all the above sources to get complete data on exposure. It is possible however, that in some situations only one of the above sources is reliable.

For example, dose of radiation received by an individual as part of medical therapy can be obtained reliably only from the medical record, information on exposure variables like blood pressure or body build or blood chemistry values can be obtained only by medical investigation. Careful thought should be given deciding the most reliable source of exposure information.

A very important aspect of obtaining exposure data is the question of ‘Non-response’ from individuals in a group. One should almost always expect some degree of non-response from population groups. The true relationship between exposure and outcome will be affected in the cohort study only if the non-response is selected with respect to both exposure and outcome.

Since this is not easy to determine, special efforts are needed:

(a) To collect exposure data on sub sample of non-respondents,

(b) To compare non-respondents with respondents on general information like Age, Sex, etc., which can be obtained from out­side the source of exposure information and

(c) Follow-up, where feasible, of non-respondents (as well as respondents) to compare outcomes like deaths or hospital admission, etc. in the two groups.

Selection of Comparison Groups:

1. Internal Comparison Groups:

A single cohort is selected for the study and its members are classified into exposure categories, on the basis of information obtained on these at entry to the study.

For example, all pregnant women in a defined geographic area during a specified period from the cohort, to study the association of pre-natal factors (including past pregnancy history), and low birth weight. The women can, on entry to the study, be classified according to their pre-natal status and comparisons made.

2. Comparison with Population Rates:

Outcomes in a study cohort may be compared with experience of the general population during the period of the study. This is particularly true when ‘special exposure cohorts’—like the ones in Japan after atomic bombing —are studied.

3. Comparison with another Specially Selected Cohort:

An unexposed group similar in demographic characteristics to the exposed group may be selected.

Outcome Determination:

The procedures for ascertaining outcomes will naturally differ depending on their nature. The procedures may vary from collection of information from routine records to periodic medical examination/investigation of each member of the study and comparison groups.

It is important to note that completeness of ascertainment of outcomes should be same in both study and comparison groups. One point to be kept in mind is the possibility that the diagnosis of outcome may be influenced by exposure class. ‘Blind’ readings for outcomes with elements of subjectivity should be used wherever feasible. Objective tests should be used to assess outcomes, wherever feasible.

Interpretation:

Two Problems Need Attention:

(1) To what extent are the observed difference (or lack of difference) between the comparison groups due to methodologic difficulties, and

(2) Whether observed differences in outcome between exposure categories can be taken as reflecting causal relationship between exposure and outcome. The first is related to points discussed in the ‘Selection of the comparison cohorts’.

Strength of association, consistency in repetitive studies under differing conditions, evidence of a dose-response relation­ship, biological plausibility and other ancillary evidence need to be looked at before a ‘causal relationship’ can be informed from an epidemio­logic study. The size of the ‘relative risk’ is a better index of a causal relationship between exposure and outcome than the attributable risk.

Advantages of Cohort Studies:

Generally free from certain selection biases:

Time sequencing that is the causal factor occurring before effects occur is automatically taken care of. Since information on ‘exposure’ is collected before observing effects, interview bias is eliminated.

(2) A spectrum of outcomes from a particular exposure can be observed.

(3) Provides direct estimates of incidence rates and relative risks.

Disadvantages of Cohort Studies:

(1) Can examine only one hypothesis at a time. New hypothesis cannot be generated after the start of the study, since ‘exposure’ is the starting point for the study.

(2) Inefficient—both statistically and practically for studying rare diseases.

Essay # 2. Experimental Epidemiological Studies:

Intervention Studies:

Randomised Clinical Trials (RCT):

The Randomised Clinical Trial (RCT) differs from the Cohort study in one essential respect. The ‘exposure’ status of individuals admitted to an RCT is decided on the basis of a random allocation.

In other words, eligible individuals are randomly allocated to ‘exposure’ categories— Placebo and Treatment Groups—and the effects of exposure and non-exposure (or different degrees of exposure) on outcome during a defined period compared statistically.

The following points need attention in planning and RCT:

(1) Reason for the Study:

(a) Rationale for the study (including consideration of ethical aspects of the study).

(b) Objective(s)—Classified into ‘Primary’ and ‘Secondary’.

(2) Individuals to be Admitted to the Study:

(a) What is the universe to which the results are to be generalized.

(b) Diagnostic criteria—Reliability, validity and standardisation.

(3) Criteria for excusing individuals form admission to the RCT.

(4) Design of the Study:

(a) Procedure of random allocation Pre-Stratification, if feasible.

(b) Need for placebo groups.

(c) Need for a feasibility of ‘Double blind’ and ‘Blind’ procedures in pre-and post- treatment assessments.

(d) Treatment regimens—dose, rhythm, duration.

(e) Exclusion of individuals from trial after admission into the RCT, because of side-effects, deterioration in clinical condition, etc. Objective definitions to be used for toxicity.

(f) Any freedom to treating physician to alter mode of therapy—specifically what is not permitted.

(5) Identification and Measurement of Treatment Effects:

(a) Choice of and criteria for measurement of outcome.

(b) Standardization of measurement of outcome.

(c) Uniform assessment of the different groups.

(d) Time of final assessment and any time latitude in final assessment.

(6) Sample size

(7) Analysis