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chemotherapy, and autologous bone marrow transplantation. Lancet1989; ii: 891-95.

20 Steward WP, Scarffe JH, Dirix LY, et al. Granulocyte-macrophagecolony-stimulating factor (GM-CSF) after high-dose melphalan inpatients with advanced colon cancer. Br J Cancer 1990; 61: 749-54.

21 Nemunaitis J, Rabinowe SN, Singer JW, et al. Recombinantgranulocyte-macrophage colony-stimulating factor after autologousbone marrow transplantation for lymphoid cancer. N Engl J Med 1991;324: 1773-78.

22 Socinski MA, Cannistra SA, Elias A, Antman KH, Schnipper L,Griffin JD. Granulocyte-macrophage colony-stimulating factorexpands the circulating haemopoietic progenitor cell compartment inman. Lancet 1988; i: 1194-98.

23 Sheridan WP, Begley CG, Juttner CA, et al. Effect of peripheral-bloodprogenitor cells mobilised by filgrastim (G-CSF) on platelet recoveryafter high-dose chemotherapy. Lancet 1992; 339: 640-44.

24 Hammond WP, Price TH, Souza LM, Dale DC. Treatment for cyclicneutropenia with granulocyte colony-stimulating factor. N Engl J Med1989; 320: 1306-11.

25 Schuster MW, Liu ET, Solberg LA, et al. Granulocyte-macrophagecolony-stimulating factor (GM-CSF) for aplastic anemia (AA):preliminary results of a multi-centre randomised controlled trial. Blood1990; 76: 47 (abstr).

26 Miles SA, Mitsuyasu RT, Moreno J, et al. Combined therapy withrecombinant granulocyte colony-stimulating factor and erythropoietindecreases hematologic toxicity from zidovudine. Blood 1991; 77:2109-17.

27 Pluda JM, Yarchoan R, Smith PD, et al. Subcutaneous recombinantgranulocyte-macrophage colony-stimulating factor used as a singleagent and in an alternating regimen with azidothymidine in leukopenicpatients with severe human immunodefficiency virus infection. Blood1990; 76: 463-72.

28 Wodzinski MA, Hampton KK, Reilly JT. Differential effects ofG-CSF and GM-CSF in acquired chronic neutropenia. Br J Haematol1991; 77: 249-250.

29 Lieschke GJ, Cebon J, Morstyn G. Characterisation of the clinicaleffects after the first dose of bacterially synthesised recombinanthuman granulocyte-macrophage colony-stimulating factor. Blood 1989;74: 2634-43.

30 Bennett CL, Greenberg P, Gulati SC, Advani R, Bonnem E.GM-CSF decreased duration of cytopenia and hospitalization, andin-hospital costs in patients with Hodgkin’s disease treated withhigh-dose chemotherapy and autologous bone marrow transfusion(ABMT). Blood 1990; 76: 132 (abstr).

31 Sachs L. The control of growth and differentiation in normal andleukemic blood cells. Cancer 1990; 65: 2196-206.

Making comparisons

Center for Clinical Epidemiology and Biostatistics, University ofPennsylvania, 317R Nursing Education Building/6095, Philadelphia,Pennsylvania, 19104, USA (Jeane Ann Grisso MD)

When making clinical choices, we often rely on standardapproaches taught when we trained or are influenced bycolleagues, experience, or the latest reports. Unfortunately,initial reports often mislead because the study did notinclude a comparison group or included an inappropriateone. In the 1950s an accepted method of treating anginainvolved ligation of the internal mammary artery. Initialreports (involving series of treated patients) showed sub-stantial improvement in symptoms. However, in 1959, astudy randomising patients to a "sham" operation or toligation reported equal improvements in both groups2 andthe procedure fell into disrepute. In the 1960s, coronaryartery bypass surgery (CABG) was introduced for thetreatment of coronary artery disease. Initial reports (againbased on series of treated patients) showed that anginasymptoms improved significantly and mortality rates werelower than those in past groups of patients treated withdrugs. Although subsequent controlled trials demonstratedthat mortality rates were improved in only a subset ofpatients, the number of CABGs in the US increased morethan sixfold from 1976 to 1986.3,4 Comparisons are crucial inreaching conclusions about what is normal or abnormal orin determining whether a treatment improves the course ofthe disease.The strength of the experimental method lies in the

investigator’s control over the selection of treatment

groups, nature of interventions, and management duringfollow-up, in order to make unbiased comparisons. How-ever, many clinical questions cannot be ethically or

logistically addressed by experimental studies. Does

postmenopausal oestrogen therapy cause breast cancer?Does passive smoking cause respiratory illness? To addressthese questions, observational studies are designed in whichthe investigator does not control the therapy or exposurebut attempts to make valid comparisons between individ-uals with or without diseases or between those "naturally"

Panel: Advantages and disadvantages of major- epidemiological study designsAdapted from Strom,$with perm issfon.

158

exposed or unexposed to a factor of interest. The panelsummarises the advantages and disadvantages of thedifferent experimental and observational designs.

Observational studiesIn an observational study, the investigator is not able tospecify the exposures or treatments for study subjects.Observational studies are often further divided into

descriptive (case reports, case series) and analytic (cross-sectional, case-control, and cohort) studies. Data from

descriptive studies can be used to generate hypotheses.Analytic studies are designed specifically to test hypothesesabout risk factors, allowing more definitive conclusions.

Case reports and case seriesCase reports provide detailed clinical and laboratory resultsfor 1 patient or a small group of patients whereas case seriesare descriptions of larger numbers. Patients often comefrom a single hospital or medical practice and thus may notbe typical. Without a comparison group, we cannot becertain which features in the description of the patients areunique to the exposure or disease. For example, the originalcase series of what was later identified as AIDS includedsmall numbers of young homosexual men with unusual

disorders, such as Kaposi’s sarcoma.6 It was not possiblefrom these studies to know whether AIDS was associatedwith being young and homosexual without comparing therates of disease in other groups. Case reports and case seriesare used to raise hypotheses and data from laboratorystudies may contribute to our understanding of themechanisms of disease.

Cross-sectional studies

In a cross-sectional study, exposure to a possible risk andthe presence of disease at one point in time are assessed in apopulation group. Prevalence (number of cases of existingdisease per population at risk) can be compared amongthose with and without current exposure to the factor ofinterest. For instance, comparison of the estimated preva-lence of AIDS for different population groups thought tovary in risk showed that the highest rates were found amongyoung single men in certain geographical regions in the USas well as among patients who had received multiple bloodtransfusions or who had haemophilia.7

In a cross-sectional study, the timing of exposure andonset of disease cannot be determined. For example, wemight learn that obese individuals are more likely to haveosteoarthritis than non-obese individuals.8 However, in across-sectional study it would not be clear whether obesitycauses osteoarthritis or whether people with osteoarthritistend to get less exercise and therefore become obese. Thus,for these studies, interpretation of measures of associationbetween exposures and disease is often limited because ofthe uncertain temporal sequence. Nevertheless, prevalencestudies are useful to describe the extent of the disease and

exposures in the population, especially for chronic diseases.

Ecological studiesThese studies evaluate correlations or trends based oninformation derived from groups. Usually, routinely col-lected information on disease rates is compared withavailable data on the general level of exposure for selectedgeographical areas-eg, male circumcision practices indifferent countries in Africa have been compared with theHIV seroprevalence rates in those countries.9 Comparisons

Figure: Cohort and case-control studiesThese studies provide similar information but approach data fromopposite directions. (Reprinted from Strom,l2 with permission.)

may be made across geographical regions or over time(called analyses of secular trends or time-series studies).For example, a secular trend analysis demonstrated acorrelation between sales over time of Rely tampons and thetoxic shock syndrome epidemic.10

Ecological studies are most useful in raising hypotheses.However, these studies lack data on individuals and cannotidentify a factor as a true cause, since other factors mayaccount for the association. Inappropriate conclusionsabout associations identified from ecological data are oftenreferred to as the "ecological fallacy". 11

Case-control studies

The use and understanding of case-control studies aremajor developments in epidemiology. Case-control studiescompare persons with a disease with controls without the

disease, looking for differences in previous exposures

(figure). As an example, women with hip fractures havebeen compared with controls without hip fractures, withassessment of previous use of postmenopausal oestrogentherapy. Such studies have generally demonstrated a strongprotective association between the use of oestrogen therapyand hip fractures.13,14 Case-control studies usually obtaininformation on exposures retrospectively. Thus, research-ers must rely on memory and the accuracy and complete-ness of medical records. The difficulty of assessment ofexposure, often termed information bias, is a majorlimitation to case-control research.Another challenge is the selection of controls. The

objective is to choose individuals representative of thetheoretical population to which the cases belong. This isoften defined as the population in which its members, hadthey developed disease, would have been selected as cases.Controls should be selected independently of the exposuresof interest. One of the first case-control studies of AIDSincluded, as a control group, homosexual men seeking carein a sexually transmitted disease (STD) clinic.15 The

proportion who reported anal intercourse in the previousyear did not differ between cases and controls because thecontrol group was selected on the basis of being homosexualand sexually active.

Case-control studies can be particularly useful in

studying multiple possible causes of a single disease,because several different potential risk factors can be

investigated with the same cases and controls. This designis also useful when studying a rare disease because it

guarantees a sufficient number of cases while maintainingsmaller sample sizes than those needed for cohort studies.

159

Cohort studies

Two or more groups who are free of the disease under studyand differ according to exposure to a potential cause of thedisease are observed over time to compare the incidence ofdisease in each group (figure). Cohort studies can be doneconcurrently or not, by creating exposure groups from pastrecords and following them up from that time to thepresent. Persons are recruited disease-free on the basis of

exposure, and their subsequent disease course is then

studied. For instance, the Centers for Disease Control andPrevention has followed health-care workers to assess HIVinfection rates in workers exposed to the blood of HIV-infected patients.16Usually both the exposed and unexposed cohort mem-

bers come from a similar subgroup of the population. Insome studies, however, an external comparison group, suchas the general population, is used. General populationgroups are not ideal in studies evaluating occupationalexposures, because workers are usually healthier than thegeneral population (the healthy worker effect)-healthierpeople are more likely to get jobs and continue to work. Forexample, in a study of carbon disulphide exposure andcoronary heart disease, exposed workers had higher mor-tality rates from coronary heart disease than workers in thepaper industry in the same town, but the rates in the paperindustry workers were lower than those in the generalpopulation. 17Concurrent cohort studies have fewer problems with

information bias than case-control studies because of the

prospective collection of data. Cohort studies are particu-larly useful to study multiple possible outcomes from asingle exposure. Finally, exposure-specific rates of diseasecan be calculated directly. Unfortunately, a cohort design isoften limited because the incidence of disease is low, whichmeans that a large number of people must be followed up fora long time before results are available.

Experimental studiesIn an experiment the investigator assigns the exposure tothe subject. Thus ethical constraints limit experimentalstudies to evaluation of therapeutic or preventive interven-tions. There are two forms of epidemiological experiments.

Clinical trials

Individuals in the experimental or treated group are

exposed to the intervention and individuals in the control orcomparison groups are not. The clinical course of bothgroups is observed and any differences in outcome areattributed to the intervention. Numerous strategies havebeen used to assemble comparison groups. Subjects mayserve as their own comparators before intervention.

Comparison groups may be selected from another geo-graphical location or time (historical controls). Theseapproaches are limited by the fact that location and time arealmost always related to outcomes, making it difficult todisentangle the true effect of the intervention. Sacks et al18reviewed clinical trials to see if the use of concurrent as

opposed to historical controls produced different results.Only 20% of trials with a concurrent, randomised controlgroup found the experimental treatment to be better,compared with 79% of trials with historical controls. Ingeneral, choosing concurrent controls from a similar settingreduces this problem to a minimum. To evaluate the uniqueeffects of a clinical intervention without bias, the best way toassemble a comparison group is to assign subjects randomlyto either the treatment or control group. Randomised

controlled trials can occasionally be used to study the causeof disease. For example, to answer the question of whetherSTDs enhance the transmission of HIV infection, someinvestigators advocate randomised trials to assess whetherintervention against STDs reduces the transmission ofHIV.19Randomised clinical trials, however, are expensive and

artificial: often only a select subgroup of patients isincluded. Common exclusion criteria are atypical disease,the presence of other diseases, an unusually poor prognosis,and contra-indications to one of the treatments .20 Becausethe group of patients is restricted, generalising from theresults to other patients is limited. Randomisation may not,by chance alone, result in similar groups. Differences

arising after randomisation (such as in drop-out rates,participants receiving other interventions unequally, and inadherence) can also bias study results.

Community trialsThese involve an intervention on a community-wide ratherthan an individual basis and are necessary when theintervention cannot be easily implemented separately forindividuals. Examples include interventions involving themedia, or the use of water fluoridation to prevent dentalcaries. Community trials are often designed to preventdisease occurrence and thus can be large and expensive.The main problem is assignment of the intervention toensure similarity of the groups.

ConclusionsIn general, we proceed from case reports and case series,which suggest an association, to case-control studies, whichexplore the association. If a question warrants the delay,cohorts can be studied. Finally, clinical trials can be used toanswer questions about therapeutic or preventive efficacy.For instance, as the AIDS epidemic unfolded, the firstpublished reports were of clinical observations of smallnumbers (case series). These were followed by descriptiveepidemiological analyses of the prevalence of the disease indifferent population groups and in different geographicalareas (cross-sectional and ecological studies). Next, case-control and cohort studies were designed to identify riskfactors and prognostic factors. Now, trials are being done toevaluate treatment and preventive measures.Although each design has an appropriate role in contri-

buting to our understanding of health and disease, clini-cians should be aware of the limitations of each type of

study. In any one study, a reported association may haveoccurred by chance, and even a true association may notapply to all population groups. Findings should thereforebe evaluated critically and in the context of existingknowledge.

References

1 McGoon DC. Prologue: from whence? Cardiovasc Clin 1987; 17:xvii-xv.

2 Cobb LA, Thomas GI, Dillard DH, Merendino KA, Bruce RA. Anevaluation of internal-mammary-artery ligation by a double-blindtechnic. N Engl J Med 1959; 260: 1115-18.

3 Lytle BW, Gosgrove D, Loop FD. Future implications of currenttrends in bypass surgery. Cardiovasc Clin 1991; 21: 265-78.

4 Murphy ML, Hultgren HKN, Detre K, et al. A preliminary report ofsurvival data of the randomised Veterans Administration CooperationStudy. N Engl J Med 1977; 297: 621-27.

5 Strom BL. Pharmacoepidemiology. New York: Churchill Livingstone,1989: 13-26.

6 Anonymous. Kaposi’s sarcoma and pneumocystis pneumonia amonghomosexual men-New York City and California. MMWR 1981; 30(July 3): 305.

160

7 Hardy AM, AllenJR, Morgan WM, Curran JW. The incidence rate ofacquired immunodeficiency syndrome in selected populations. JAMA1985; 253: 215-20.

8 Kelsey J, Thompson WD, Evans AS. Methods in observationalepidemiology. Oxford: OUP, 1986: 3.

9 Bongaarts J, Reining P, Way P, Conant F. The relationship betweenmale circumcision and HIV infection in African populations. AIDS1989; 3: 373-77.

10 Anonymous. Toxic-shock syndrome—United States, 1970-1980.MMWR 1981; 30: 25-28.

11 Michael M III, Boyce WT, Wilcox AJ. Biomedical bestiary: anepidemiology guide to flaws and fallacies in the medical literature.Boston: Little, Brown and Co, 1984.

12 Strom BL. Medical databases in postmarketing drug surveillance.Trends Pharmacol Sci 1986; 7: 377.

13 Williams AR, Weiss NS, Ure CL, et al. Effect of weight, smoking, andestrogen use on the risk of hip and forearm fractures inpostmenopausal women. Obstet Gynecol 1982; 60: 695-99.

14 Kreiger N, Kelsey JL, Holford TR, O’Connor T. An epidemiologic

study of hip fracture in postmenopausal women. Am J Epidemiol 1982;116: 141-48.

15 Jaffe HW, Choi KW, Thomas PA, et al. National case-control study ofKaposi’s sarcoma and Pneumocystis carinii pneumonia in homosexualmen: part I, epidemiological results. Ann Intern Med 1983; 99:145-51.

16 Henderson DK, Fahey BJ, Willy M, et al. Risk for occupationaltransmission of human immunodeficiency virus type 1 (HIV-1)associated with clinical exposure: a prospective study. Ann Intern Med1990; 113: 740-46.

17 Wen CP, Tsai SP, Gibson RL. Anatomy of the healthy worker effect: acritical review. J Occup Med 1983; 25: 283-89.

18 Sacks H, Chalmer TC, Smith H Jr. Randomized versus historicalcontrols for clinical trials. Am J Med 1982; 72: 233-40.

19 Mertens TE, Hayes RJ, Smith PG. Epidemiological methods to studythe interaction between HIV infection and other sexually transmitteddiseases. AIDS 1990; 4: 57-65.

20 Fletcher RH, Fletcher SW, Wagner EH. Clinical epidemiology: theessentials. 2nd ed. Baltimore: Williams & Wilkins, 1988.

Viewpoint

What have teachers learnt?

Social and Behavioral Sciences Branch, Technical Support Division,International Health Program Office, Centers for Disease Controland Prevention, F-03, Clifton Road, Atlanta, Georgia 30333, USA(J Bryce EdD, J F Naimoli MPH); London School of Hygiene and TropicalMedicine (F Cutts MD); and Save the Children Fund, London, UK(F Cutts, M Beesley)

Correspondence to: Dr Jennifer Bryce

"No-one doubts the contribution that training can make todevelopment of all kinds. Training is essential, obviously so.The doubt comes over its contribution in practice.Complaints are growing about its effectiveness and waste...Yet training continues to be in fashion. No self-respectingcountry does without it."

Rolf P Lynton, Udai Pareek, 19671

25 years after they were written, these words are stillrelevant. Why? Have we learnt nothing, or are we unable toapply what we have learnt? We raise a series of questionsthat we hope will stimulate assessment and improvement oftraining programmes for health workers in developingcountries.

Is training the only solution?A common response to difficulties with delivery of healthservices is to initiate or expand an in-service trainingprogramme. In-service training can improve healthworkers’ knowledge and skills,2.3 but does not guaranteethat they will provide adequate services.4-6 In studies inCote d’lvoire and Niger State, Nigeria trained healthworkers knew how to treat children with fever anddiarrhoea correctly, but could not do so because of

shortages of oral rehydration salts in Nigeria andantimalarial drugs in Cote d’lvoire. Similarly, in Zambeziaprovince, Mozambique, over 50% of difficulties identifiedduring supervision were attributable to inadequate logisticsupport. For training to improve services, new skills mustbe complemented by available commodities and otheressential resources.4

Workshops: the magic wandWorkshops are attractive. They are discrete, time-limitedactivities; funds can be disbursed quickly; and trainees canbe counted easily. The ultimate measure of effective

training, however, is improvement on the job.l In Nigeria,for example, an observational study (Continuing EducationUnit, Ministry of Health, Niger State, Nigeria, un-

published) assessed health worker performance in demon-strating the preparation of oral rehydration solution toparents of children with diarrhoea. 82% of parents whoconsulted trained and supervised health workers received ademonstration, compared with 33 % of those who consulteduntrained and unsupervised workers. To improve on-the-job performance, workshops must be part of a continuousprocess of training and supervision. Planners must assessthe learning needs of trainees, develop curricula to meetthese needs, provide various opportunities for learning, andmonitor and follow up participants.

Standard curricula: penny-wise andpound-foolish?Train large numbers of people and train them quickly!International agencies have developed and disseminatedstandard curricula to attain these goals. The potentialadvantages are clear. Standard curricula can be targetedto different tiers in the health delivery system and

adapted to local situations by trained "facilitators".

They can be incorporated quickly into training pro-

grammes at low cost to ministries of health and used to

promote procedures consistent with international healthstandards.

However, prepackaged materials have limitations. Theirpredetermined content, format, and instructions to trainersmay not be appropriate for the skill levels of trainees. Sometarget-setting manuals have seriously overestimated thequantitative skills of peripheral health workers.4 Manage-ment training materials do not always recognise the limitedbackground, skills, and decision-making powers of districtpersonnel.8 8

Training materials should respond to changing publichealth needs and priorities, which vary widely amongcountries. Although there are increasing efforts to supportlocal adaptation of standard materials, successful trainingwill require that national capacity in designing instructionalprogrammes and materials be built Up.1.9,10 For example,capacity for curriculum development was expanded amongMinistry of Health personnel in the Central African

Republic through the development of training in immunis-