1. THE STUDY DESIGNS
A STUDY DESIGN IS A SPECIFIC PLAN OR PROTOCOL FOR CONDUCTING THE STUDY, WHICH ALLOWS THE INVESTIGATOR TO TRANSLATE THE CONCEPTUAL HYPOTHESIS INTO AN OPERATIONAL ONE.

2. CRITERIA FOR SELECTION OF THE RIGHT DESIGN
RELEVANT :DESIGN ALLOWS YOU TO ANSWER YOUR RESEARCH QUESTION
NOVEL :DESIGN ALLOWS MEANINGFUL CONTRIBUTION TO EXISTING KNOWLEDGE ~ NEW INSIGHTS

3. FEASIBLE
DESIGN ALLOWS STUDY TO BE DONE WITHIN AVAILABLE TIME AND FUNDS
SIMPLE
ALWAYS AVOID ALL UNNECESSARY COMPLEXITIES

4. THE BASIS OF A GOOD RESEARCH IS AN APPROPRIATE STUDY DESIGN
MANY CLASSIFICATIONS FOR THE RESEARCH DESIGNS RESULTING IN CONFUSION AND DILEMA

5. THE STUDY DESIGNS ARE CLASSIFIED INTO:
DESCRIPTIVE STUDY DESIGNS: AIM TO SEARCH FOR FACTS.
ANALYTICAL STUDY DESIGNS: AIM TO SEARCH FOR CAUSES.
EXPERIMENTAL STUDY DESIGNS: AIM TO PUT SOLUTION INTO ACTIONS.

6. MAIN TYPES OF EPIDEMIOLOGIC STUDIES
STUDIES PREVENTIONS AND TREATMENTS FOR DISEASES; INVESTIGATOR ACTIVELY MANIPULATES WHICH GROUPS RECEIVE THE AGENT UNDER STUDY.
EXPERIMENTAL
STUDIES CAUSES, PREVENTIONS,
AND TREATMENTS FOR DISEASES;
INVESTIGATOR PASSIVELY OBSERVES
AS NATURE TAKES ITS COURSE.
OBSERVATIONAL
TYPICALLY EXAMINES MULTIPLE HEALTH EFFECTS OF AN EXPOSURE; SUBJECTS ARE DEFINED ACCORDING TO THEIR EXPOSURE LEVELS AND FOLLOWED FOR DISEASE
OCCURRENCE
COHORT.
TYPICALLY EXAMINES MULTIPLE EXPOSURES IN RELATION TO A DISEASE; SUBJECTS ARE DEFINED AS CASES AND CONTROLS, AND EXPOSURE HISTORIES ARE COMPARED
CASE–CONTROL

7. EXAMINES RELATIONSHIP BETWEEN EXPOSURE AND DISEASE PREVALENCE IN A DEFINED POPULATION AT A SINGLE POINT IN TIME.
CROSS-SECTIONAL
EXAMINES RELATIONSHIP BETWEEN EXPOSURE AND DISEASE WITH POPULATION-LEVEL RATHER THAN INDIVIDUAL-LEVEL DATA.
ECOLOGICAL

8. EPIDEMIOLOGIC STUDY DESIGNS

9. Hierarchy of Epidemiologic Study Design

10. STUDY DESIGNS THE DESCRIPTIVE STUDY DESIGNS:
THESE STUDIES ARE CONCERNED WITH OBSERVING THE DISEASE DISTRIBUTION OR HEALTH RELATED EVENTS AND EVENTS SEEM TO BE ASSOCIATED WITH THE DISEASE.

11. WHEN IS THE DISEASE OCCURRING?
(TIME DISTRIBUTION)
WHERE IS THE DISEASE OCCURRING?
(PLACE DISTRIBUTION)
WHO IS AFFECTED? (PERSON DISTRIBUTION)

15. THE PROCEDURES IN THE DESCRIPTIVE STUDIES
DEFINE THE DISEASE UNDER THE STUDY.
DEFINE THE POPULATION UNDER THE STUDY.
DESCRIBE THE DISEASE BY TIME, PERSON AND PLACE.
MEASUREMENT OF THE DISEASE.
COMPARING WITH KNOWN INDICES.
FORMULATION OF AETIOLOGICAL HYPOTHESIS.

16. SURVEY
A SURVEY IS A SIMPLE DECRIPTIVE DESIGN AND USUALLY DEFINED AS COLLECTION OF DATA FROM ALL INDIVIDUALS OR A SAMPLE OF INDIVIDUALS CHOSEN TO BE REPRESENTATIVE OF THE POPULATION FROM WHICH THEY ARE DRAWN.

17. PREVALENCE RATE STUDY, DISEASE FREQUENCY STUDY.
CROSS SECTIONAL STUDY
PREVALENCE RATE STUDY, DISEASE FREQUENCY STUDY.
THE RELATIONSHIP BETWEEN THE DISEASE & OTHER VARIABLES OF INTEREST AS THEY EXIST AT ONE PARTICULAR POINT OF TIME

18. ). ).

19. CROSS-SECTIONAL STUDIES DETERMINE THE PRESENCE (PREVALENCE) OF BOTH EXPOSURE AND DISEASE IN THE SUBJECTS AND
DO NOT DETERMINE THE DEVELOPMENT OF DISEASE OR RISK OF DISEASE (INCIDENCE).

20. MOREOVER, SINCE BOTH EXPOSURE AND DISEASE ARE DETERMINED IN AN INDIVIDUAL AT THE SAME POINT IN TIME,
IT IS NOT POSSIBLE TO ESTABLISH THE TEMPORAL RELATION BETWEEN EXPOSURE AND DISEASE—

21. THAT IS, THAT THE EXPOSURE PRECEDED THE DISEASE, WHICH WOULD BE NECESSARY FOR DRAWING ANY CAUSAL INFERENCE.

22. THUS, A RESEARCHER MAY USE A CROSS-SECTIONAL STUDY TO DETERMINE THE RELATIONSHIP BETWEEN A PERSONAL CHARACTERISTIC THAT DOES NOT CHANGE OVER TIME, SUCH AS BLOOD GROUPING, AND EXISTENCE OF A DISEASE, .

23. SUCH AS APLASTIC ANEMIA, BY EXAMINING INDIVIDUALS AND DETERMINING THEIR BLOOD TYPES AND WHETHER THEY SUFFER FROM APLASTIC ANEMIA

24. DESIGN OF A CROSS-SECTIONAL STUDY
DEFINED POPULATION
GATHER DATA ON EXPOSURE& DISEASE
NOT
EXPOSED
DO NOT
HAVE
DISEASE
EXPOSED
DO NOT
HAVE
DISEASE
NOT
EXPOSED
HAVE
DISEASE
EXPOSED;
HAVE
DISEASE

25. THE FINDINGS CAN BE VIEWED IN 2X2 TABLE AS FOLLOWS:
INTERPRETATION
THE FINDINGS CAN BE VIEWED IN 2X2 TABLE AS FOLLOWS: NO
DISEASE
DISEASE
DISEASE
NO DISEASE
EXPOSED b b a
EXPOSED a d
NOT
EXPOSED d
NOT
EXPOSED c c

27. CROSS SECTIONAL STUDY OF ELEVATED BLOOD PRESSURE
MEASURE THE B.P. AMONG THE STUDY POPULATION: PREVALENCE OF HYPERTENSION.
COLLECT DATA ON AGE, SEX, SOCIAL CLASS AND OCCUPATION.
DETERMINE HOW PREVALENCE OF HYPERTENSION IS RELATED TO THESE VARIABLES

28. BENEFITS OF CROSS-SECTIONAL STUDY::
FEASIBILITY: THEY ARE EASY TO CARRY OUT
THE ASSOCIATED COST IS LOW.
THEY MAY BE CARRIED OUT IN A RELATIVELY SHORT TIME,

29. CALCULATED: IT IS OFTEN THE MOST RELEVANT MEASURE FOR
4. PREVALENCE CAN BE
CALCULATED: IT IS OFTEN THE
MOST RELEVANT MEASURE FOR
BURDEN OF DISEASE, INFORMING
HEALTH CARE STRATEGIES.

30. 5. THE MEASURE OF ASSOCIATION IS READILY AVAILABLE, FROM WHICH ONE CAN CALCULATE THE ODDS RATIO FOR THE PREVALENT DISEASE.

31. LONGITUDINAL STUDY DESIGNS
OBSERVATIONS ARE REPEATED IN THE SAME POPULATION OVER A PROLONGED PERIOD OF TIME BY MEANS OF FOLLOW UP EXAMINATIONS. THESE ARE USEFUL:
STUDY THE NATURAL HISTORY OF THE DISEASE.
IDENTIFY THE RISK FACTORS.
DETERMINE THE INCIDENCE RATE.

32. STUDY THE EFFECTS OF NEW INTERVENTIONS OR TRENDS OF BEHAVIOUR

33. CASE STUDY A FORM OF SINGLE STUDY RESEARCH.
UNDERTAKEN ON AN INDIVIDUAL CASE WHICH IS TYPICAL FOR THE TARGETED CASES I.E. A CASE OF CONGENITAL ANAMOLY.
HISTORY OF EXPOSURE CAN BE TRACED.

34. FORMULATION OF HYPOYHESIS
AN EPIDEMIOLOGICAL HYPOTHESIS SHOULD SPECIFY:
THE POPULATION: THE CHARACTERISTICS OF PERSONS.
THE SPECIFIC CAUSE.
THE DISEASE.
THE DOSE RESPONSE RELATIONSHIP.
THE TIME RESPONSE RELATIONSHIP

35. EXAMPLES CIGARETTE SMOKING CAUSES CA LUNG.
THE SMOKING OF CIGARETTES PER DAY CAUSES LUNG CANCER IN 10 % OF SMOKERS AFTER 20 YEARS OF EXPOSURE

36. USES OF DESCRIPTIVE STUDIES
PROVIDE DATA ABOUT DISEASE LOAD.
FORMULATION OF ETIOLOGICAL HYPOTHESES.
DATA FOR PLANNING, EVALUATION OF CURATIVE & PREVENTIVE SERVICES.
CONTRIBUTE TO RESEARCH.

37. ANALYTICAL STUDY DESIGNS
THE SUBJECT OF INTEREST IN THE ANALYTICAL DESIGNS IS THE INDIVIDUAL RATHER THAN THE WHOLE POPULATION.
THE AIM IS TO TEST ETIOLOGICAL HYPOTHESIS.

38. TWO DISTINCT TYPES OF ANALYTICAL STUDIES: CASE-CONTROL COHORT

39. THE CASE CONTROL STUDY

40. OFTEN CALLED RETROSPECTIVE STUDIES.
IT IS BETTER NOT TO USE THIS TERM.
THE COMMON FEATURES:
1. BOTH EXPOSURE & OUTCOME HAVE OCCURRED.
2. PROCEEDS BACKWARD FROM EFFECT TO CAUSE.
3. PRESENCE OF A CONTROL GROUP.

41. BASIC STEPS SELECTION OF THE CASES & CONTROLS. MATCHING.
MEASUREMENT OF EXPOSURE TO THE VARIABLE UNDER INVESTIGATION.
ANALYSIS & INTERPRETATION

42. DESIGN OF A CASE CONTROL STUDY
EXPOSED
NOT EXPOSED
EXPOSED
NOT EXPOSED
DISEASE
NO DISEASE
CONTROLS
CASES

43. SELECTION OF CASES &CONTROLS
THIS IS THE MOST IMPORTANT STEP.
IT INVOLVES TWO SPECIFICATIONS:
1. DIAGNOSTIC CRITERIA:
SPECIFIC DIAGNOSTIC CRITERIA OF THE DISEASE, ITS STAGING ARE TO BE STATED CLEARLY.

44. 2. ELIGIBILITY CRITERIA:
THE REQUIREMENT THAT ONLY NEWLY DIAGNOSED CASES RATHER THAN OLD ONES

45. THE CHRONOLOGIC ORDER OF THE EXPOSURE AND DISEASE, WHICH IS EASY TO ELUCIDATE IN COHORT STUDIES, MAY BE UNCERTAIN FROM THE RESULTS OF A CASE–CONTROL STUDY BECAUSE IT MAY NOT BE POSSIBLE TO KNOW IF THE EXPOSURE OCCURRED BEFORE THE DISEASE.

46. IT MAY BE DIFFICULT TO KNOW WHAT HAPPENED FIRST:
.FOR EXAMPLE, IF A CASE–CONTROL STUDY OF ASTHMA IN HIGH SCHOOL STUDENTS DEMONSTRATES AN ASSOCIATION WITH CAT OWNERSHIP,
IT MAY BE DIFFICULT TO KNOW WHAT HAPPENED FIRST:

47. THE PRESENCE OF CATS OR THE FIRST ASTHMA ATTACK
THE PRESENCE OF CATS OR THE FIRST ASTHMA ATTACK. ONE CAN OFTEN OVERCOME THIS PROBLEM BY INCLUDING ONLY NEWLY DIAGNOSED CASES

48. The sources of cases:
1. Hospitals.
2. The general population
The selection of controls:
The controls must be similar to
cases as possible except for
absence of disease under
investigation.

49. THE SOURCES OF CONTROLS ARE:
1. HOSPITAL CONTROLS.
2. RELATIVES.
3. NEIGHBORHOOD CONTROLS.
4. GENERAL POPULATION.

50. HOW MANY CONTROLS ARE NEEDED?
GENERALLY ONE CONTROL IS NEEDED FOR EACH CASE. IF THE STUDY GROUP IS SMALL 2,3, OR EVEN 4 CONTROLS FOR EACH CASE IS POSSIBLE.

51. MATCHING:
DEFINED AS THE PROCESS BY WHICH WE SELECT CONTROLS IN SUCH A WAY THAT THEY ARE SIMILAR TO CASES WITH REGARDS TO CERTAIN VARIABLES(CONFOUNDING) TO ENSURE COMPARABILITY.

52. 2. INDIVIDUAL MATCHING(MATCHED PAIRS).
CASES & CONTROLS MAY DIFFER IN CHARACTERISTICS OR EXPOSURES OTHER THAN THE ONE TARGETED FOR THE STUDY.
MATCHING IS DONE EITHER AS:
GROUP MATCHING OR
2. INDIVIDUAL MATCHING(MATCHED PAIRS).

53. 1. GROUP MATCHING(FREUENCY MATCHING)
SELECTION OF CONTROLS IN SUCH A MANNER THAT THE PROPORTION OF CONTROLS WITH A CERTAIN CHARACTERISTICS IS IDENTICAL TO THE PROPORTION OF CASES WITH THE SAME CHARACTERISTIC.
THUS IF 25% OF THE CASES ARE MARRIED, THE CONTROLS WILL BE SELECTED SO THAT 25% OF THE CONTROL IS ALSO MARRIED.

54. THIS REQUIRES THAT ALL CASES SELECTED FIRSTLY.
THEN CALCULATIONS OF THE PROPORTIONS OF CERTAIN CHARACTERISTICS AMONG THE CASES. SELECTION OF A CONTROL GROUP WITH THE SAME PROPORTIONS IS MADE.

55. 2. INDIVIDUAL MATCHING(MATCHED PAIRS):
IN THIS APPROACH, FOR EACH CASE SELECTED FOR THE STUDY, A CONTROL SUBJECT IS SELECTED WHO IS SIMILAR TO THE CASE IN TERMS OF SPECIFIC VARIABLE OR VARIABLES OF CONCERN.

56. THE PROBLEMS OF MATCHING:
OVERMATCHING
THE MATCHED CHARACTERISTICS CAN NOT BE STUDIED.

57. NESTED CASE CONTROL
SUPPOSE A PROSPECTIVE COHORT STUDY WERE CONDUCTED AMONG ALMOST 90,000 WOMEN FOR THE PURPOSE OF STUDYING THE DETERMINANTS OF CANCER AND CARDIOVASCULAR DISEASE.

58. AFTER ENROLLMENT, THE WOMEN PROVIDE BASELINE INFORMATION ON A HOST OF EXPOSURES, AND THEY ALSO PROVIDE BASELINE BLOOD AND URINE SAMPLES THAT ARE FROZEN FOR POSSIBLE FUTURE USE.

59. THE WOMEN ARE THEN FOLLOWED, AND, AFTER ABOUT EIGHT YEARS, THE INVESTIGATORS WANT TO TEST THE HYPOTHESIS THAT PAST EXPOSURE TO PESTICIDES SUCH AS DDT IS A RISK FACTOR FOR BREAST CANCER.
EIGHT YEARS HAVE PASSED SINCE THE BEGINNING OF THE STUDY, AND WOMEN IN THE COHORT HAVE DEVELOPED BREAST CANCER

60. . SINCE THEY FROZE BLOOD SAMPLES AT BASELINE, THEY HAVE THE OPTION OF ANALYZING ALL OF THE BLOOD SAMPLES IN ORDER TO ASCERTAIN EXPOSURE TO DDT AT THE BEGINNING OF THE STUDY BEFORE ANY CANCERS OCCURRED.

61. ONE COULD ANALYZE ALL OF THE BLOOD SAMPLES FROM WOMEN WHO HAD DEVELOPED BREAST CANCER,
BUT JUST ANALYZE A SAMPLE OF THE NON-DISEASE WOMEN IN ORDER TO ESTIMATE THE EXPOSURE DISTRIBUTION IN THE POPULATION THAT PRODUCED THE CASES.

62. IN THIS SCENARIO THE POPULATION THAT PRODUCED THE CASES IN THE INITIAL COHORT OF 89,849 WOMEN. IF ONE WERE TO ANALYZE THE BLOOD SAMPLES OF 2,878 OF THE NON-DISEASED WOMEN (TWICE AS MANY AS THE NUMBER OF CASES)

64. IN ESSENCE, A CASE-CONTROL STRATEGY WAS USED, BUT IT WAS CONDUCTED WITHIN THE CONTEXT OF A PROSPECTIVE COHORT STUDY. THIS IS REFERRED TO AS A CASE-CONTROL STUDY "NESTED" WITHIN A COHORT STUDY.

67. ADVANTAGES:
LESS EXPENSIVE THAN ANALYSIS
OF THE FULL COHORT
DISADVANTAGES:
NON-DISEASED PERSONS FROM WHOM THE CONTROLS ARE SELECTED MAY NOT BE FULLY REPRESENTATIVE OF THE ORIGINAL COHORT DUE TO LOSS TO FOLLOW-UP OR DEATH

68. CASE COHORT STUDY
IN THE CLASSIC NESTED CASE CONTROL STUDY CONTROLS ARE CHOSEN FROM SUBJECTS WHO DID NOT DEVELOP THE DISEASE IN THE CORRESPONDING CLOSED COHORT.

69. AN ALTERNATIVE OPTION IS TO SELECT CONTROLS FROM THE MEMBERS OF THE ORIGINAL COHORT. THE RESULTING CASE CONTROL STUDY IS USUALLY REFERRED TO AS A CASE COHORT STUDY.

70. THE EXPOSURE ODDS AMONG THE SELECTED CONTROLS (B/D) SHOULD ESTIMATE THE EXPOSURE ODDS IN THE FULL COHORT (N1/N0).

71. SINCE THE OUTCOMES IN A COHORT STUDY AT PART OF THE AT-RISK SUBJECTS AT THE START OF A STUDY, IT IS POSSIBLE DISEASE CASE MIGHT ALSO BE SELECTED AS A CONTROL IN A CASE COHORT STUDY.

72. THIS PRESENTS SOME PROBLEMS IN PERFORMING TESTS OF SIGNIFICANCE AND CONFIDENCE INTERVAL ESTIMATION, BUT DOES NOT INVALIDATE THE EXPOSURE ODDS RATIO FROM THE CASE COHORT STUDY ESTIMATING THE RISK RATIO FROM THE COHORT STUDY

73. ANALYSIS: THE EXPOSURE RATE AMONG BOTH THE CASES AND THE CONTROLS.
2. ODDS RATIO:THIS RATIO CAN BE USED TO ESTIMATE THE RELATIVE RISK AS THE INCIDENCE RATE CAN NOT BE DETERMINED IN CASE-CONTROL STUDY DESIGN.

74. THUS THE CASE CONTROL STUDY IS ALWAYS SUGGESTIVE OF THE ETIOLOGICAL ASSOCIATION BETWEEN TWO VARIABLES

75. IN EPIDEMIOLOGY, ODDS OF AN ATTRIBUTE CAN BE DEFINED AS THE RESULT OF DIVIDING THE PROPORTION OF INDIVIDUALS WITH AN ATTRIBUTE BY THE PROPORTION OF INDIVIDUALS WITHOUT THE ATTRIBUTE IN A POPULATION.

76. ODDS CAN BE INTERPRETED AS THE PROBABILITY OF OCCURRENCE OF AN EVENT AS COMPARED TO THE PROBABILITY OF NONOCCURRENCE OF AN EVENT IN A POPULATION.

77. CASE-CONTROL STUDY OF SMOKING & Ca LUNG

78. 1. The exposure rate among cases= a/a+c = 33/35= 0.94x100=94%
2. The exposure rate among the controls= b/b+d=55 /82= 0.67x100=67%.

79. 3. ODDS OF EXPOSURE AMONG CASES=A/C=33/2=16.5
4. ODDS OF EXPOSURE AMONG CONTROLS=B/D=55/27=2.04
5. ODDS RATIO= A/C÷B/D = A/C X D/B=891÷110=8.1

80. INTERPRETATION:
FROM THE EXPOSURE RATES AMONG THE CASES & CONTROLS:CHI SQUARE TEST HAS TO BE USED TO CONFIRM THAT THERE IS STATISTICAL DIFFERENCE BETWEEN THE TWO VALUES. .

81. IF THE ODDS RATIO IS FOUND TO BE GREATER THAN ONE: POSITIVE ETIOLOGICAL ASSOCIATION

82. IF THE ODDS RATIO IS EQUAL TO 1: THERE IS NO ETIOLOGICAL ASSOCIATION BETWEEN THE EXPOSURE AND THE OUTCOME.

83. IF THE ODDS RATIO IS LESS THAN ONE: THERE IS NEGATIVE ASSOCIATION BETWEEN THE EXPOSURE AND THE OUTCOME. IN SOME SITUATIONS THE EXPOSURE TO THE RISK FACTOR MIGHT BE PROTECTIVE FROM THE DISEASE.

85. ADVANTAGES OF CASE-CONTROL STUDIES
APPROPRIATE FOR RARE DISEASES.
RELATIVELY QUICK.
RELATIVELY INEXPENSIVE.

86. FEW SUBJECTS.
STUDY MANY POSSIBLE CAUSES OF A SINGLE DISEASE.

87. DISADVANTAGES OF CASE-CONTROL STUDIES
RECALL DEPENDENT: INFORMATION BIAS
INCOMPLETE CONTROL OF EXTERNAL FACTORS.
DIFFICULT TO SELECT CONTROLS.

88. CAN NOT CALCULATE INCIDENCE RATES.
CAN NOT STUDY MECHANISMS OF DISEASE.
IN PRACTICE, CASE–CONTROL STUDIES ARE OFTEN AFFECTED BY SELECTION BIAS

89. SELECTION BIAS MAY BE PRESENT IF THE CONTROL GROUP DOES NOT COME FROM THE SAME POPULATION AS THE CASES.

90. FOR EXAMPLE, IF CASES OF ASTHMA ARE DRAWN FROM A POPULATION OF HIGH SCHOOL STUDENTS, AND CONTROLS WITHOUT ASTHMA ARE DRAWN FROM A POPULATION OF OLDER INDIVIDUALS WHO DO NOT ATTEND HIGH SCHOOL

91. ONE RISKS INTRODUCING A SERIOUS BIAS.
THIS REPRESENTS A PROBLEM BECAUSE THE FACTORS RELATED TO ASTHMA ARE DIFFERENT IN YOUNG AND OLDER INDIVIDUALS. CONSEQUENTLY,

92. MANY FACTORS THAT MIGHT BE FOUND TO BE ASSOCIATED WITH ASTHMA, BASED ON A STUDY OF SUCH MISMATCHED CASES AND CONTROLS, MIGHT RESULT MERELY FROM THE FACT THAT THESE TWO POPULATIONS ARE OF DIFFERENT AGE.

93. CASE CONTROL DESIGNS ARE NOT GENERALLY GOOD FOR STUDYING RARE EXPOSURES.
FOR EXAMPLE, IF WE WANT TO STUDY THE RISK OF ASTHMA FROM WORKING IN A NUCLEAR SUBMARINE SHIPYARD,

94. WE WOULD PROBABLY NOT DO A CASE CONTROL STUDY BECAUSE A VERY SMALL PROPORTION OF PEOPLE WITH ASTHMA WOULD HAVE BEEN EXPOSED TO SUCH A FACTOR.

95. CASE–CONTROL STUDIES CANNOT BE USED TO STUDY MULTIPLE DISEASES OR CONDITIONS BECAUSE IT IS NECESSARY TO GUARANTEE THAT THE CONTROL GROUP IS COMPARABLE FOR EACH DISEASE OR CONDITION SELECTED.

96. THEREFORE, IF ONE WANTS TO STUDY MORE THAN ONE DISEASE, NEW GROUPS OF CASES AND CONTROLS ARE NEEDED.

97. COHORT STUDY DESIGNS

98. IN COHORT STUDIES, THE INVESTIGATOR IDENTIFIES:
POPULATION FREE OF DISEASE (COHORT).
DETERMINES THEIR EXPOSURE STATUS.

99. FOLLOW OVER TIME TO DETERMINE THE OUTCOME IN BOTH EXPOSED AND NON-EXPOSED GROUPS.
THE INFORMATION ON EXPOSURE IS OBTAINED BEFORE THE OBSERVATION OF THE DISEASE STATUS.

100. CONCEPT OF COHORT
COHORT IS A GROUP OF PEOPLE WHO SHARE A COMMON CHARACTERISTIC OR EXPERIENCE WITHIN A DEFINED PERIOD I.E. OCCUPATION,AGE, EXPOSURE TO DRUG OR VACCINE.

101. EXAMPLES:
THE DOCTORS GRADUATED IN 1996
THE FEMALE CHILDREN BORNE IN 1995
THE WORKERS APPOINTED IN KHARTOUM NORTH ASBESTOS INDUSTRY IN 1960
ALL NURSING STAFF APPOINTED IN KTH IN YEAR 2000

102. OPEN COHORT
AN OPEN COHORT IS A DYNAMIC POPULATION WITH MIGRATION INTO AND OUT OF THE COHORT OCCURRING DURING THE FOLLOW-UP PERIOD.

103. EXPOSURE STATUS MAY CHANGE OVER TIME
SO THAT THE SAME SUBJECTS CAN CONTRIBUTE PERSON-TIME TO DIFFERENT EXPOSURE GROUPS.
EXPOSURE STATUS MAY CHANGE OVER TIME

104. The following figure shows the
general features of an open cohort study.
----D D D D D
_______________________________________Beginning End

105. CLOSED COHORT
A CLOSED COHORT HAS A COMMON STARTING POINT AND FIXED POTENTIAL PERIOD OF FOLLOW-UP FOR ALL SUBJECTS.
FOR EXAMPLE, THE FRAMINGHAM COHORT STUDY STARTED IN IT ENROLLED 5,209 SUBJECTS IN 1948 WITH THE PLAN TO FOLLOW ALL SUBJECTS FOR 20 YEARS..

106. EXPOSURE IS DEFINED AT THE START OF THE FOLLOW-UP AND DOES NOT CHANGE OVER TIME. THERE ARE NO LOSSES-TO-FOLLOW-UP.
THE OUTCOME MEASURE FOR SUCH COHORTS IS EITHER THE CUMULATIVE INCIDENCE OR THE INCIDENCE RATE

108. A FIXED COHORT IS SIMILAR TO A CLOSED COHORT WITH THE EXCEPTION THAT THERE ARE SOME SUBJECTS WHO ARE LOST-TO-FOLLOW-UP.
THE FRAMINGHAM HEART STUDY WITH THE OUTCOME OF ALL-CAUSE MORTALITY AND SEX AS AN EXPOSURE IS AN EXAMPLE OF A CLOSED COHORT AS THERE IS COMPLETE ASCERTAINMENT OF THIS OUTCOME ON ALL SUBJECTS

109. ON THE OTHER HAND, IF THE OUTCOME IS THE DEVELOPMENT OF CHD THEN IT SHOULD BE CONSIDERED AS A FIXED COHORT AS SOME SUBJECTS ARE LOST-TO-FOLLOW-UP AND THEIR SUBSEQUENT DEVELOPMENT OF CHD IS UNKNOWN..

110. ALSO, THERE ARE OTHER SUBJECTS WHO DIE FROM NON-CHD CAUSES (COMPETING RISK) AND THEREFORE ARE NO LONGER AT RISK FOR DEVELOPING CHD

111. THE COMMON FEATURES OF COHORT STUDY DESIGNS
1. THE COHORTS ARE IDENTIFIED PRIOR TO THE APPEARANCE OF THE DISEASE UNDER INVESTIGATION.

112. 3. THE STUDY PROCEEDS FORWARDS FROM CAUSE TO EFFECT.
2. FOLLOW UP TO DETERMINE THE INCIDENCE OF THE DISEASE.
3. THE STUDY PROCEEDS FORWARDS FROM CAUSE TO EFFECT.

113. HOW CAN WE IDENTIFY THE COHORTS?
1. WE CAN CREATE A STUDY POPULATION THE BASIS OF WHETHER OR NOT THEY ARE EXPOSED.

114. 2. WE CAN SELECT A DEFINED POPULATION BEFORE ANY OF ITS MEMBERS BECOME EXPOSED OR BEFORE THEIR EXPOSURES ARE IDENTIFIED.

115. DESIGN OF A COHORT STUDY
NOT EXPOSED
EXPOSED
DO NOT
DEVELOP
DISEASE
DEVELOP
DISEASE
DO NOT
DEVELOP
DISEASE
DEVELOP
DISEASE

116. INDICATIONS OF COHORT STUDIES
1. WHEN THERE IS STRONG SUSPICION BETWEEN EXPOSURE AND DISEASE.
2. WHEN THE EXPOSURE IS RARE BUT INCIDENCE IS HIGH AMONG EXPOSED.

117. 3. WHEN ATTRITION OF THE STUDY GROUPS CAN BE MINIMIZED.
4. WHEN AMPLE FUNDS ARE AVAILABLE

118. TYPES OF COHORT STUDIES
1. CONCURRENT PROSPECTIVE COHORT STUDY.
THE INVESTIGATOR IDENTIFIES THE ORIGINAL POPULATION AT THE BEGINNING OF THE STUDY AND THEN FOLLOW TILL THE DISEASE APPEARS. .

119. 2. RETROSPECTIVE COHORT STUDY.
THE COHORTS IDENTIFIED FROM PREVIOUS RECORDS & THEN DIVIDED IN TO EXPOSED AND NON-EXPOSED, THEN DECIDE WHO DEVELOPS AND WHO DOES NOT DEVELOP THE DISEASE.

120. 3. RETROSPECTIVE-PROSPECTIVE COHORT STUDY.
THE COHORTS IDENTIFIED FROM PREVIOUS RECORDS.
DIVIDED INTO EXPOSED AND NON-EXPOSED.
FOLLOW UP OVER A PERIOD OF TIME TO DETERMINE THE INCIDENCE OF THE DISEASE

122. ELEMENTS OF A COHORT STUDY
1. SELECTION OF THE STUDY SUBJECTS.
2. OBTAINING DATA ON EXPOSURE
3. SELECTION OF COMPARISON GROUPS.
4. FOLLOW UP.
5. ANALYSIS.
6. INTERPRETATION.

123. SELECTION OF STUDY SUBJECTS
THE STUDY SUBJECTS CAN BE OBTAINED FROM:
FROM THE GENERAL POPULATION IF THE EXPOSURE & THE OUTCOME IS FREQUENT.
FROM THE SPECIAL GROUPS IF THE EXPOSURE AND THE OUTCOME IS LESS FREQUENT.

124. OBTAINING DATA ON EXPOSURE
THE DATA ON EXPOSURE CAN BE OBTAINED FROM:
THE COHORT MEMBERS.
REVIEW OF DOCUMENTS.
MEDICAL EXAMINATION OR SPECIAL TESTS.
ENVIRONMENTAL SURVEYS.

125. SELECTION OF COMPARISON GROUPS
THE COMPARISON GROUPS CAN BE OBTAINED FROM:
THE MEMBERS OF THE SAME COHORT AS DIVIDED INTO EXPOSED AND NON-EXPOSED.

126. EXTERNAL GROUP I.E. NON-SMOKERS.
GENERAL POPULATION FROM WHICH THE COHORT IS DERIVED

127. FOLLOW UP REVIEW OF THE PHYSICIAN,S AND HOSPITAL RECORDS.
THE FOLLOWING PROCEDURES ARE REQUIRED FOR FOLLOW UP:
PERIODIC MEDICAL EXAMINATION.
REVIEW OF THE PHYSICIAN,S AND HOSPITAL RECORDS.

128. ROUTINE SURVEILLANCE OF THE DEATH RECORDS.
MAILED AND ED QUESTIONNAIRES, TELEPHONE CALLS, PERIODIC HOME VISITS ON ANNUAL BASIS.

129. The collected data will be analyzed in terms of:
ANALYSIS
The collected data will be analyzed in terms of:
Incidence rate of disease among both exposed & non-exposed.
Estimation of risk.

130. RELATIVE RISK:
THIS IS THE RATIO THAT MEASURES THE STRENGTH OF ASSOCIATION BETWEEN SUSPECTED CAUSE AND EFFECT.
THE RR IS A MEASURE OF THE
RELATIVE MAGNITUDE OF THE
INCIDENCE IN THE EXPOSED AND
THE INCIDENCE IN THE
NONEXPOSED.

131. RR = 1 MEANS THAT THE INCIDENCE IN THE EXPOSED IS THE SAME AS THE INCIDENCE IN THE NON-EXPOSED, AND SO THERE IS NO EVIDENT ASSOCIATION BETWEEN EXPOSURE AND DISEASE.

132. RR > 1 DENOTES A LARGER INCIDENCE IN THE EXPOSED THAN THE NONEXPOSED.
THUS EXPOSURE TO THE FACTOR SEEMS TO INCREASE THE PROBABILITY OF DEVELOPING THE DISEASE.

133. WITH THE SAME REASONING, RR < 1 DENOTES A SMALLER INCIDENCE IN THE EXPOSED AS COMPARED TO THE NONEXPOSED.
THUS EXPOSURE TO THE FACTOR SEEMS TO DECREASE THE PROBABILITY OF DEVELOPING THE DISEASE.

135. ATTRIBUTABLE RISK: IT IS EXPRESSED AS %.
THIS IS THE DIFFERENCE IN INCIDENCE OF DISEASE OR DEATH BETWEEN EXPOSED & NON-EXPOSED GROUP.
IT IS EXPRESSED AS %.

136. IT MEASURES THE IMPACT THAT REMOVAL OF A CERTAIN FACTOR WILL HAVE ON THE INCIDENCE OF THE DISEASE.

137. SMOKING & CA LUNG-COHORT STUDY

138. INCIDENCE RATE OF CA LUNG AMONG SMOKERS= A/A+B=70/7000= 10/1000
INCIDENCE RATE OF CA LUNG AMONG NON-SMOKERS= C/C+D= 3/3000= 1/1000

139. RELATIVE RISK=
INCIDENCE OF DISEASE AMONG EXPOSED/INCIDENCE AMONG NON-EXPOSED= 10/1=10.

140. ATTRIBUTABLE RISK “EXCESS RISK FOR THE EXPOSED GROUP COMPARED WITH THE NON-EXPOSED GROUP= INCIDENCE RATE AMONG EXPOSED-INCIDENCE RATE AMONG NON-EXPOSED/INCIDENCE RATE AMONG EXPOSED= 10-1x100=90%

141. ADVANTAGES OF COHORT STUDIES
COMPLETE DATA ON CASES & STAGES.
STUDY OF MORE THAN ONE EFFECT OF EXPOSURE.
CALCULATE & COMPARE RATES IN EXPOSED & NON-EXPOSE.
QUALITY CONTROL OF DATA

142. DISADVANTAGES OF COHORT STUDIES
NEED LARGE NUMBERS
MANY YEARS.
CHANGES OF CIRCUMSTANCES.
EXPENSIVE.
INCOMPLETE CONTROL OF EXTERNAL FACTORS.
ATTRITION

143. EXPERIMENTAL STUDY DESIGNS

144. IN EXPERIMENTAL RESEARCH, THE STUDY SUBJECTS ARE OBSERVED UNDER PREDETERMINED CONDITIONS USING CAREFULLY DESIGNED APPROACHES TO DATA & SPECIMENS.

145. THE EXPERIMENTAL STUDY DESIGNS DIFFER FROM THE ANALYTICAL STUDY DESIGNS:
THE CONDITIONS IN WHICH THE STUDY IS CARRIED ARE UNDER DIRECT CONTROL OF THE INVESTIGATOR.

146. THE EXPERIMENTAL STUDIES INVOLVE SOME ACTION OR INTERVENTION OR MANIPULATION IN THE EXPERIMENT GROUP WHILE MAKING NO CHANGE IN THE CONTROL GROUP.

147. IN ANALYTICAL STUDIES, NO ACTION BUT ONLY OBSERVATION OF THE NATURAL COURSE OF EVENTS OR OUTCOMES.

148. THE AIMS OF EXPERIMENTAL STUDIES:
1. TO PROVIDE SCIENTIFIC EVIDENCE OF ETIOLOGICAL OR RISK FACTORS TO PERMIT MODIFICATION OR CONTROL OF DISEASE.

149. 2. TO PROVIDE A METHOD OF MEASURING THE EFFECTIVENESS OR EFFICIENCY OF THE HEALTH SERVICES FOR PREVENTION, CONTROL & TREATMENT OF DISEASE AND TO IMPROVE THE HEALTH OF THE COMMUNITY.

150. THE DISADVANTAGES OF THE EXPERIMENTAL STUDIES:
They are costly.
Ethical problems.
Feasibility.

151. THE FEATURES OF THE EXPERIMENTAL STUDY DESIGNS:
RANDOM ALLOCATION OF INDIVIDUALS TO EXPERIMENTAL & CONTROL GROUPS.
SYSTEMATIC MANIPULATION OF THE EXPERIMENTAL GROUP.

152. CONTROL OVER THE OTHER IMPORTANT FACTORS AFFECTING EXPERIMENTAL & CONTROL GROUPS.
MEASUREMENT OF SOME OUTCOME VARIABLES WITH WHICH TO COMPARE TWO GROUPS.

153. TYPES OF EXPERIMENTAL STUDIES:
1. RANDOMIZED CONTROL TRIALS:
THOSE INVOLVED A PROCESS OF RANDOM ALLOCATION. .

154. 2. NON-RANDOMIZED TRIALS:
THOSE DEPARTING FROM STRICT RANDOMIZATION FOR PRACTICAL PURPOSES BUT IN SUCH A MANNER THAT NON-RANDOMIZATION DOES NOT SERIOUSLY AFFECT THE THEORETICAL BASIS OF CONCLUSIONS

155. THE QUASI-EXPERIMENTAL STUDY DESIGNS:
IN THIS DESIGN THE CONTROL OVER THE EXTERNAL FACTORS IS NOT POSSIBLE AND THIS MIGHT ALTER THE OUTCOME VARIABLES.

156. THE RANDOMIZED CONTROLLED TRIALS
THOSE TRIALS ARE USED FOR ASSESSMENT OF METHODS OF TREATMENT AND PREVENTION.

157. THE BASIC STEPS IN CONDUCT OF RANDOMIZED CONTROLLED TRIALS:
1. DRAWING A PROTOCOL.
2. SELECTING REFERENCE & EXPERIMENTAL POPULATION.
3. RANDOMIZATION.
4. MANIPULATION OR INTERVENTION

158. 5. FOLLOW UP. 6. ASSESSMENT OF THE OUTCOME.

159. DESIGN OF A RANDOMIZED CLINICAL CONTROL TRIAL
REFERENCE
POPULATION
RANDOM
SELECTION
EXPERIMENTAL
POPULATION
RANDOMIZATION
CURRENT
TREATMENT
NEW
TREATMENT
NOT
IMPROVED
NOT
IMPROVED
IMPROVED
IMPROVED

160. THE PROTOCL ONE OF THE ESSENTIAL FEATURES OF THE RANDOMIZED TRIALS.
THE PROTOCOL SPECIFIES:
THE OBJECTIVES.
THE SELECTION CRITERIA.
THE SAMPLE SIZE.
THE PROCEDURES OF ALLOCATION OF THE SUBJECTS INTO EXPERIMENTAL AND CONTROL GROUPS.

161. 6. THE TREATMENT APPLIED:HOW, WHERE AND TO WHAT TYPES OF PATIENTS.
7. THE DETAILS OF THE SCIENTIFIC TECHNIQUES AND INVESTIGATIONS.
Once a protocol has been evolved, it should be strictly adhered to throughout the study.

162. SELECTION OF THE REFERENCE & THE EXPERIMENTAL POPULATIONS
THE REFERENCE POPULATION:
IT IS THE POPULATION TO WHICH THE FINDINGS OF THE TRIAL, IF FOUND TO BE SUCCESSFUL, ARE EXPECTED TO BE APPLICABLE.

163. THE EXPERIMENTAL POPULATION:
THE EXPERIMENTAL (STUDY) POPULATION IS DERIVED FROM THE REFERENCE POPULATION.
IT IS THE ACTUAL POPULATION THAT PARTICIPATES IN THE EXPERIMENTAL STUDY.

164. IT SHOULD BE RANDOMLY SELECTED FROM THE REFERENCE POPULATION.

165. IF THE STUDY POPULATION DIFFERS FROM THE REFERENCE POPULATION, IT MAY NOT BE POSSIBLE TO GENERALIZE THE FINDINGS TO THE REFERENCE POPULATION.

166. THEY MUST GIVE INFORMED CONSENT.
THE PARTICIPANTS OR THE VOLUNTEERS OF THE EXPERIMENT MUST FULFILL THE FOLLOWING CRITERIA:
THEY MUST GIVE INFORMED CONSENT.

167. THEY SHOULD BE REPRESENTATIVE OF THE REFERENCE POPULATION.
THEY SHOULD BE ELIGIBLE OR QUALIFIED FOR THE TRIAL

168. RANDOMIZATION:
RANDOMIZATION IS THE STATISTICAL PROCEDURE BY WHICH THE PARTICIPANTS ARE ALLOCATED INTO GROUPS USUALLY CALLED STUDY & CONTROL GROUPS TO RECEIVE OR NOT TO RECEIVE AN EXPERIMENTAL OR THERAPEUTIC PROCEDURE OR INTERVENTION.

169. RANDOMIZATION AIMS TO MAKE THE GROUPS COMPARABLE.

170. RANDOMIZATION ENSURES THAT THE INVESTIGATOR HAS NO CONTROL OVER THE ALLOCATION OF THE PARTICIPANTS TO EITHER THE STUDY OR CONTROL GROUP, THUS ELIMINATING THE SELECTION BIAS.

171. EVERY INDIVIDUAL HAS AN EQUAL CHANCE OF BEING ALLOCATED INTO EITHER GROUP.
RANDOMIZATION IS BEST DONE BY USING STATISTICAL RANDOM TABLE.

172. THE ESSENTIAL DIFFERENCE BETWEEN A RANDOMIZED TRIAL AND ANALYTICAL STUDY IS THAT:
IN THE LATTER THERE IS NO RANDOMIZATION BECAUSE DIFFERENTIATION INTO CASES & CONTROLS EXPOSED AND NON-EXPOSED GROUPS HAS ALREADY TAKEN PLACE.

173. THUS THE ONLY OPTION LEFT TO ENSURE COMPARABILITY IN ANALYTICAL STUDIES IS BY MATCHING.

174. MANIPULATION:
MANIPULATION OR INTERVENTION IS USUALLY DONE BY APPLICATION OR WITHDRAWAL OF THE SUSPECTED FACTOR E.G. DRUGS, VACCINE OR DIETARY FACTOR. .

175. THIS MANIPULATION CREATES AN INDEPENDENT VARIABLE (DRUG, VACCINE OR NEW PROCEDURE) WHOSE EFFECT IS THEN DETERMINED BY THE MEASUREMENT OF THE FINAL OUTCOME WHICH CONSTITUTES THE DEPENDENT VARIABLE E.G. INCIDENCE OF DISEASE, RECOVERY

176. FOLLOW UP:
THIS INCLUDES EXAMINATION OF THE STUDY & CONTROL GROUPS SUBJECTS AT DEFINED INTERVALS OF TIME IN STANDARD MANNER UNDER THE SAME CONDITIONS IN THE SAME TIME FRAME TILL THE FINAL ASSESSMENT.

177. THE MAIN DIFFICULTIES ENCOUNTERED IN THE FOLLOW UP PROCESS INCLUDE:
ATTRITION, DEATH, MIGRATION, DISPLACEMENT AND LOSS OF INTEREST.

178. ASSESSMENT THE FINAL ASSESSMENT OF THE TRIAL IS CARRIED IN TERMS OF:
POSITIVE RESULTS: THESE INCLUDE THE BENEFITS OF THE EXPERIMENTAL STUDY SUCH AS REDUCED INCIDENCE OF THE DISEASE OR SEVERITY OF THE DISEASE, COST OF HEALTH SERVICES OR OTHER APPROPRIATE OUTCOME.

179. NEGATIVE RESULTS: THESE INCLUDE THE SEVERITY & FREQUENCY OF SIDE-EFFECTS AND COMPLICATIONS.
THE INCIDENCE OF POSITIVE/NEGATIVE RESULTS IS COMPARED IN BOTH GROUPS AND THE DIFFERENCES ARE TESTED STATISTICALLY.

180. BIAS
Bias is the systematic difference between observed results and the actual results.
Sources of bias:
1. Participant’s bias:
The participants report subjectively that they feel better or improved if they knew that they were receiving new treatment.

181. 2.OBSERVER’S BIAS:
THE INFLUENCE OF THE INVESTIGATOR MEASURING THE OUTCOME OF THE TRIAL IF HE KNEW BEFOREHAND THE PARTICULAR PROCEDURE TO WHICH THE PATIENT HAS BEEN SUBJECTED.

182. 3. THERE MAY BE BIAS IN EVALUATION AS THE INVESTIGATOR MAY INVOLUNTARILY GIVE FAVORABLE REPORT OF THE OUTCOME OF THE STUDY.

183. HOW TO REDUCE THE SOURCES OF BIAS? 1. RANDOMIZATION. 2. BLINDING.

184. BLINDING IS CARRIED IN THREE WAYS:
1. SINGLE BLIND TRIAL:THE TRIAL IS SO PLANNED THAT THE PARTICIPANT IS NOT AWARE WHETHER HE BELONGS TO THE STUDY OR CONTROL GROUP.

185. 2. DOUBLE BLIND TRIAL: THE TRIAL IS SO PLANNED THAT NETHER THE DOCTOR NOR THE PARTICIPANT IS AWARE OF THE GROUP ALLOCATION AND TREATMENT RECEIVED.

186. 3. TRIPLE-BLIND TRIAL:
THE TRIAL IS SO PLANNED THAT THE PARTICIPANT, THE INVESTIGATOR& THE PERSON ANALYZING THE DATA ARE ALL BLIND. THIS IS THE IDEAL BUT DOUBLE-BLINDING IS THE MOST COMMONLY USED.

187. TYPES OF RANDOMIZED TRIALS:.
1. CLINICAL TRIALS:
THESE TRIALS CONCERNED WITH EVALUATING THE EFFICACY OF NEW DRUGS OR OTHER THERAPEUTIC PROCEDURES SUCH AS SURGERY, PHYSIOTHERAPY AND IONIZING RADIATION.

188. 2.Preventive trials:
IN GENERAL THE TERM PREVENTIVE TRIALS IMPLIES TRIALS OF PRIMARY PREVENTIVE MEASURES.
THE TRIALS ARE DESIGNED TO PREVENT OR ELIMINATE DISEASE ON AN EXPERIMENTAL BASIS.

189. THE MOST FREQUENTLY OCCURRING TYPE OF PREVENTIVE TRIALS ARE THE TRIALS OF VACCINES AND CHEMO PROPHYLAXIS.

190. DESIGN OF A RANDOMIZED PREVENTIVE CONTROL TRIAL
REFERENCE
POPULATION
RANDOM
SELECTION
EXPERIMENTAL
POPULATION
RANDOMIZATION
DO NOT
RECEIVE
VACCINE
RECEIVED
VACCINE NO
DISEASE NO
DISEASE
DISEASED
DISEASED

191. PHASES OF CLINICAL TRIALS
A PRPOERLY PLANNED AND IMPLEMENTED CLINICAL TRIAL IS A POWERFUL TECHNIQUE FOR ASSESSING THE EFFECTIVENESS OF AN INTERVENTION

192. A CLINICAL TRIAL IS A PROSPECTIVE STUDY COMPARING THE EFFECT OF INTERVENTION(S) AGAINST A CONTROL IN HUMAN BEINGS
A CLINICAL TRIAL IS PROSPECTIVE RATHER THAN RETROSPECTIVE

193. STUDY PARTICIPANTS MUST BE FOLLOWED FOREWARD IN TIME.
FOLLOW UP OF THE STUDY SUBJECTS OVERTIME WITHOUT ACTIVE INTERVENTION MAY MEASURE THE NATURAL HISTORY OF DISEASE BUT THIS IS NOT A CLINICAL TRIAL

194. CLINICAL TRIALS HAVE SEVERAL STEPS:
PHASE (1):
THE FIRST STEP OR PHASE IS TO UNDERSTAND HOW WELL THE INTERVENTION CAN BE TOLERATED IN A SMALL NUMBER OF INDIVIDUALS

195. IT DOES NOT MEET THE STANDARD DEFINITION OF A CLINICAL TRIAL.
MOST PHASE 1 DESIGNS ARE RELATIVELY SIMPLE.

196. THIS DOSE IS USUALLY CALLED MAXIMALLY TOLERATED DOSE MTD
EVALUATING DRUGS, NEEDS FIRST STEP IS TO ESTIMATE HOW A DOSE CAN BE ADMINISTERED BEFORE UNACCEPABLE TOXICITY IS EXPERIENCED BY PATIENTS.
THIS DOSE IS USUALLY CALLED MAXIMALLY TOLERATED DOSE MTD

197. PHASE 11 TRIALS:
ONCE THE MTD IS ESTABLISHED: THE NEXT STEP IS TO EVALUATE WHETHER THE DRUG HAS ANY BIOLOGICAL EFFECT AND TO ESTIMATE THE RATE OF ADVERSE EFFECTS.

198. IF THE DESIGN OF PHASE 1 HAS NOT BEEN ADEQUATE, THE INVESTIGATOR MAY EVALUATE THE DOSE.
PHASE 11 DESIGN DEPENDS ON THE QUALITY OF ADEQUACY OF PHASE 1

199. THE DESIGN USUALLY ENCOUNTERS A LIMITED NUMBER OF PATIENTS 14 AND THEN THE RESPONSE RATE IS ESTIMATED

200. IF THE RESPONSE RATE IS LESS THAN THE 20%: THE DRUG IS OMITTED.
IF THE RESPONES IS GREATER THAN 20%: MORE PATIENTS ARE RECRUITED ACCORDING TO THE PRECISION DESIRED: USUALLY 10-20

201. PHASE 111/1V: THESE ARE CLINICAL TRIALS AS DEFINED.
PHASE 111 TRIALS HAVE A SHORT PERIOD OF EVALUATION
FOCUS ON EFFECTIVENESS BUT KNOWLEDGE ON SAFETY IS ALSO NECESSARY

202. LONG-TERM STUDIES WHICH DO NOT INVOLVE CONTROL GROUPS TO EVALUATE PROPERLY THE PROPER ROLE OF AN INTERVENTION: ARE CALLED PHASE 1V TRIALS