The development and translation of assessment instruments in psychiatry is a lengthy, multi-phase and complex process, which becomes increasingly important in a uniting but still multilingual Europe. A lower or questionable quality of any of the developmental phases makes the interpretation and publication of research based on these instruments a difficult if not impossible task. The major aim of the European Commission BIOMED funded multi-site study called EPSILON (European Psychiatric Services: Inputs Linked to Outcome and Needs) was to produce standardised versions in several European languages of instruments measuring five key concepts in mental health service research (Reference Becker, Knapp and KnudsenBecker et al, 1999): (a) the Camberwell Assessment of Need (CAN), measuring the needs for care; (b) the Involvement Evaluation Questionnaire (IEQ), assessing family or caregiving burden; (c) the Verona Service Satisfaction Scale (VSSS), measuring satisfaction with services; (d) the Lancashire Quality of Life Profile (LQoLP), assessing the quality of life of the patient; and (e) the Client Socio-Demographic and Service Receipt Inventory (CSSRI). This paper describes the background, rationale and design of the reliability study. Its main focus will be on the importance of reliable instruments, theoretical considerations of reliability testing and the general reliability testing procedure of the study.
BACKGROUND
Throughout Europe there is a trend away from hospital-based services towards a variety of locally based community care services for people with severe mental health problems. These community-based services are organisationally more complex, and potentially more demanding on the families of the patients and the local communities. However, they are more likely than hospital-based services to successfully target services to the needs of the most disabled patients, and, as a consequence, are more likely to produce better outcomes at lower treatment and social costs.
Because of its organisational complexity compared with hospital services, community care is more difficult to evaluate. For a proper evaluation of these newer forms of service, a multi-dimensional approach is required (Reference Knudsen and ThornicroftKnudsen & Thornicroft, 1996), which, in addition to well-known patient characteristics like psychopathology and social functioning, should also focus on concepts like needs for care, satisfaction with services, quality of life and family or caregiving burden. To measure these concepts, several instruments have been developed in Europe during the past decade (Reference ScheneSchene, 1994; Reference TansellaTansella, 1997). After scientific work on the validity and reliability of the original versions, these instruments were translated into several languages. However, as a consequence of the urgent need to measure the process and the outcome of community care, in most cases the psychometric qualities of these translations (cultural validity and reliability) were not adequately tested.
AIMS AND METHOD OF THE EPSILON STUDY
In an attempt to attack this scientific omission, the aim of this study was to produce standardised versions in five European languages (Danish, Dutch, English, Italian, Spanish) of the five instruments mentioned. These instruments have been developed by different research groups in the past 5-10 years. Because of the quality of the developmental processes, the reliability and validity of each of the original instruments for its particular cultural setting was considered to be good (for the development of each instrument, see the separate reliability papers in this supplement : Reference Chisholm, Knapp and KnudsenChisholm et al, 2000; Reference McCrone, Leese and ThornicroftMcCrone et al, 2000; Reference Ruggeri, Lasalvia and Dall'AgnolaRuggeri et al, 2000; Reference van Wijngaarden, Schene and Koetervan Wijngaarden et al, 2000; Reference Gaite, Vázquez-Barquero and Arriaga ArrizabalagaGaite et al, 2000). So the study was focused on generalising the validity and reliability of these instruments over the five European cultural settings. This was done in three steps: (a) translation and back-translation according to World Health Organization standards into the five European languages (Reference Sartorius, Kuyken, Orley and KuykenSartorius & Kuyken, 1994); (b) a review of translations by the focus group technique (Reference Vázquez-Barquero and GaiteVázquez-Barquero & Gaite, 1996) for cultural validity and applicability, and adaptation of the instruments if necessary (for a more detailed description see Reference Knudsen, Vázquez-Barquero and WelcherKnudsen et al, 2000, this supplement); and (c) evaluation of the instruments' reliability (Reference Schene, Koeter and van WijngaardenSchene et al, 1997). This paper discusses the third step of the procedure.
RELIABILITY
Theoretical considerations
The quality of any measurement instrument (such as an interview or questionnaire) depends on the validity and reliability of the instrument. ‘ Validity’ refers to the extent to which a (test) score matches the actual construct it has to measure, or in other words to the bias or impact of systematic errors on test scores. ‘Reliability’ refers to the extent to which the results of a test can be replicated if the same individuals are tested again under similar circumstances, or, in other words, to the precision and reproducibility or the influence of unsystematic (random) errors on the test scores.
Two approaches to reliability can be distinguished: modern test theory (item response theory) and classical test theory. The item response approach makes a comparison of an instrument's performance over different populations possible because, contrary to classical test theory, reliability coefficients in item response theory are not influenced by the population variance. This advantage, however, is diminished by the assumptions concerning the quality of data (e.g. monotonically increasing tracelines, local independence of the items, and - in most cases - dichotomous items), limiting the applicability of an item response approach to those relatively scarce data that fulfil these constraints. In addition, a relatively large number of respondents at each site (200-1000) is needed for an item response approach. The relatively severe constraints on the data, as well as the sample size requirements, made the item response approach not feasible for the EPSILON Study (Reference Donner and EliasziwDonner & Eliasziw, 1987). So it was decided to base the reliability analyses in this study on classical test theory.
In classical test theory, a person's observed score can be expressed as
(X i=observed score, T i=true score and E i=the error or random, non-systematic part of the score). In psychology and psychiatry, ‘gold standards’ are lacking, and so a person's true score is defined as his/her theoretical average score over an infinite number of administrations of the same test. Given the assumptions of classical test theory, the variability in the observed scores in a group of respondents (σ2 X ) is composed of the variability in their ‘true’ scores (σ2 T ) and an error component (σ2 E ). The reliability of a test (ρxx) is defined as the ratio between true score variance and observed score variance (σ2 T /σ2 X ). Test reliability defined in the ‘classical’ way therefore depends to a large extent on the true score variance of the population in which the test was originally developed (since σ2 X =σ2 T +σ2 E ). If the test is used in another population with a different true score variance (for instance, it might have a lower variance because this population is more homogeneous with respect to the construct under study) the reliability will become lower. For example, in a sample where the error component (σ2 E ) is 0.10 and the true score variance (σ2 T ) is 40, reliability will be 0.80. In another sample with the same error component of 10 but a true score variance of 20, reliability will be 0.66. This ‘population’ dependence of the reliability coefficient makes comparisons between populations tricky. Differences in reliability between two populations can be caused by differences in precision of the instrument between the populations under study (σ2 E ), or by differences in true score variance of the populations under study (σ2 T ).
One way of handling this problem is the use of the standard error of the mean (s.e.)m, which equals the error component of variance (σ
E
). The (s.e.)m, unlike a reliability coefficient, is independent of the true score variance 
, where (s.d.)
x
is the standard deviation between subjects). The (s.e.)m can be interpreted in two ways. First, it can be used to indicate limits within which the observed score would be expected to lie. For example, if the true score were 10, and the (s.e.)m were 5, for 68% of the time one would expected observed score to lie in the range 5-15. Second, it indicates the difference to be expected on retesting or between two raters. For example, if the first observed score were 10, the second observed score would be expected to lie in the range 2.9-17.1 
for 68% of the time. The (s.e.)m is therefore particularly useful when assessing the precision of an instrument in absolute terms, in relation to an individual measurement.
Importance of reliable instruments
The reliability of instruments is of importance for at least two reasons.
-
(a) Low reliability automatically implies low validity. The reliability of a measure is defined as the squared correlation between the observed score X and the true score
, a correlation which in case of perfect reliability equals 1. The validity of a measure is defined as the correlation between the true score, T, and the construct one wants to measure, Y. If the validity is perfect, the true score is identical to the actual construct (T=Y). Differences between observed scores and Y are only caused by random errors (and hence ). In this case the validity coefficient equals the square root of the reliability coefficient. If validity is not perfect, the value of the validity coefficient will be lower than the square root of reliability; so the reliability coefficient sets the upper limit for the validity coefficient (). -
(b) Unreliability masks the true relationship between constructs under study. If the error components of the observed scores are uncorrelated, the maximal theoretical possible correlation between two unreliable measures is the square root of the product of their respective reliabilities :
. So research for relationships between different constructs is seriously hampered by unreliable operationalisations of these constructs.
, a correlation which in case of perfect reliability equals 1. The validity of a measure is defined as the correlation between the true score, T, and the construct one wants to measure, Y. If the validity is perfect, the true score is identical to the actual construct (T=Y). Differences between observed scores and Y are only caused by random errors (and hence 
). In this case the validity coefficient equals the square root of the reliability coefficient. If validity is not perfect, the value of the validity coefficient will be lower than the square root of reliability; so the reliability coefficient sets the upper limit for the validity coefficient (
).
. So research for relationships between different constructs is seriously hampered by unreliable operationalisations of these constructs.Reliability assessment procedures in the EPSILON Study
In this study three different reliability measures are used, depending on the nature of the instruments involved and the way they are administered (interviews v. questionnaires): (a) Cronbach's α for scales and sub-scales consisting of more than one item; (b) Cohen's κ to estimate the interrater reliability and test-retest reliability of single items; and (c) the intraclass correlation coefficient (ICC) to estimate the interrater reliability and test-retest reliability of scales and sub-scales.
Cronbach's α
If a particular construct is measured by means of a scale consisting of two or more items, measures of internal consistency can be used to estimate the reliability of the scale. A simple measure of internal consistency is the split-half reliability of a scale, obtained by randomly dividing the scale into two sub-scales and calculating the correlation between those two sub-scales. The Cronbach's α statistic can be considered as the average of all possible split-half reliabilities of a scale. It is sometimes referred to as the internal consistency coefficient (Reference Streiner and NormanStreiner & Norman, 1995). However one should take into account that α is a function not only of the mean inter-item correlation (a real measure of the internal consistency) but also of the number of items of the scale; hence an increase in α does not automatically mean an increase in the internal consistency. Therefore α can more properly be interpreted as the lower limit of the proportion of variance in the test scores explained by common factors underlying item performance (Reference Crocker and AlginaCrocker & Algina, 1986), such that the lower limit of the reliability - the ‘true’ reliability - is at least as high as α (Reference DunnDunn, 1989).
The value of α may be expected to substantially underestimate the reliability if different items measure different quantities (Reference ShroutShrout, 1998); as, for example, in the CAN, where differences between needs in different areas reduce the value of α but do not necessarily imply poor reliability. On the other hand, the errors in individual items in the same scale at the same time may well be positively correlated, which will tend to inflate α relative to the reliability.
Interrater reliability: Cohen's κ and intraclass correlation coefficients
Compared with self-report data, interview data have an additional source of variance that may account for lack of consistency: the interviewer. Although one would prefer an interview, when administered by two different interviewers to the same patient, to produce approximately the same scores - under the assumption that the patient has not changed over time - this is not always the case. Standardisation and structuring of the interview, combined with a thorough training, should in practice diminish the influence of any idiosyncratic characteristics of the interviewers.
The generalisability of the interview scores over interviewers can be estimated by computing a measure of interrater reliability which quantifies the extent to which the information obtained by a specific interviewer can be generalised to other (potential) interviewers. Cohen's κ coefficient is used for categorical data in this study (for variables with more than two categories, a weighted version of the κ coefficient can be used), and ICC for data with at least an ordinal level of measurement.
Strictly speaking, κ is a measure of agreement, not a reliability coefficient, since it is not defined as a ratio of true score variance to observed score variance. κ is defined as (Po - Pe/(1 - Pe) where Po is the observed agreement and Pe is the chance agreement: a value of 0 means that the observed agreement is exactly what could be expected by chance, while a value of 1 indicates perfect agreement.
The ICC is computed as the ratio of between-patient variance to total variance, which is the sum of between-patient variance and error variance (Reference Streiner and NormanStreiner & Norman, 1995). If systematic bias is present (for example, if one rater systematically reports higher scores than the other), then this is reflected in the ICC.
Test-retest reliability: intraclass correlation coefficient and Cohen's κ
The test-retest reliability coefficient, sometimes called the stability coefficient, tests the assumption that when a characteristic is measured twice, both measures must lead to comparable results. However, test-retest reliability is only a valid indicator of the reliability of an instrument if the characteristic under study has not changed in the interval between testing and retesting. This means either a relatively stable characteristic (like intelligence, personality, socioeconomic status) or a short time interval. A short time interval between test administrations, however, may produce biased (inflated) reliability coefficients, due to the effect of memory.
Crocker & Algina (Reference Crocker and Algina1986) ask two questions with regard to the interpretation of a stability coefficient as a measure of reliability. First, does a low value of the stability coefficient imply that the test is unreliable or that the construct itself has changed over time ? Second, to what extent is an examinee's behaviour or perception of the situation altered by the test administration ? In the EPSILON Study we are dealing with relatively stable constructs, so low stability will indicate low reliability. However, some effect of the test administration on a patient's behaviour and/or perception cannot be ruled out. For this reason, the value of the stability coefficient must be considered as a lower limit for the test-retest reliability.
As was the case with interrater reliability, the kind of test-retest statistics used in this study depends on the nature of the instruments. In the case of items containing categorical data (weighted), κ is used. In the case of instruments containing ordinal scales and sub-scales, the ICC statistic is used.
Interviewer characteristics may cause systematic differences between test and retest interview scores. Although reliability, strictly speaking, only refers to unsystematic differences, we believe that the interviewer-related systematic differences should also be taken into account when evaluating the test-retest reliability of the instruments. For this reason we do not use statistics insensitive to systematic change, like rank order correlations, but κ and ICC.
Reliability analysis: design and procedure
Study sites
For this study, researchers from five centres geographically and culturally spread across the European Union (Amsterdam, Copenhagen, London, Santander and Verona) joined forces. All had experience in health services research, mental health epidemiology, and the development and cross-cultural adaptation of research instruments, and had access to mental health services providing care for local catchment areas.
Sample
The following criteria were applied in all centres.
Inclusion criteria : aged between 18 and 65, inclusive, with an ICD-10 F20 diagnosis (schizophrenia), in contact with mental health services during the 3-month period preceding the start of the study.
Exclusion criteria : currently residing in prison, secure residential services or hostels for long-term patients; co-existing learning disability (mental retardation); primary dementia or other severe organic disorder; and extended in-patient treatment episodes longer than one year. These criteria were laid down in order to avoid bias between sites due to variation in the population of patients in long-term institutional care, and to concentrate on those in current ‘active’ care by specialist mental health teams.
First, administrative prevalence samples of people with ICD-10 diagnosis of any of F20 to F25 in contact with mental health services were identified either from psychiatric case registers (Copenhagen and Verona) or from the case-loads of local specialist mental health services (inpatient, out-patient and community). Second, cases identified were diagnosed using the item group checklist (IGC) of the Schedule for Clinical Assessment in Neuropsychiatry (SCAN) (Reference WingWorld Health Organization, 1992). Only patients with an ICD-10 F20 (schizophrenia) research diagnosis were included in the study. The numbers of patients varied from 52 to 107 between sites, with a total of 404.
For test-retest reliability a randomly selected subsample was tested twice within an interval of 1-2 weeks. The sample sizes differed between sites, ranging from 21 to 77 for the IEQ and from 46 to 81 for the LQoLP. We refer the reader to the separate reliability papers in this supplement for more detailed information (Reference Chisholm, Knapp and KnudsenChisholm et al, 2000; Reference Gaite, Vázquez-Barquero and Arriaga ArrizabalagaGaite et al, 2000; Reference McCrone, Leese and ThornicroftMcCrone et al, 2000; Reference Ruggeri, Lasalvia and Dall'AgnolaRuggeri et al, 2000; Reference van Wijngaarden, Schene and Koetervan Wijngaarden et al, 2000).
Core study instruments
The assessment of needs was made using the Camberwell Assessment of Need (CAN) (Reference Phelan, Slade and ThornicroftPhelan et al, 1995), which is an interviewer-administered instrument which comprises 22 individual domains of need. The Involvement Evaluation Questionnaire (IEQ) (Reference Schene and van WijngaardenSchene & van Wijngaarden, 1992) is an 81-item instrument which measures the consequences of psychiatric disorders for relatives of the patient. Caregiving consequences are summarised in four scales: tension, worrying, urging and supervision. The Verona Service Satisfaction Scale (VSSS) (Reference Ruggeri and Dall'AgnolaRuggeri & Dall'Agnola, 1993) is a self-administered instrument comprising seven domains : global satisfaction, skill and behaviour, information, access, efficacy, intervention and relatives' support. The Lancashire Quality of Life Profile (LQoLP) (Reference OliverOliver, 1991; Reference Oliver, Huxley, Priebe and KaiserOliver et al, 1997) is an interview which assesses both objective and subjective quality of life on nine dimensions: work/education, leisure/participation, religion, finances, living situation, legal and safety, family relations, social relations and health. The CSSRI-EU, an adaptation of the Client Service Receipt Inventory (CSRI) (Reference Beecham, Knapp, Thornicroft, Brewin and WingBeecham & Knapp, 1992), is an interview in which socio-demographic data, accommodation, employment, income and all health, social, education and criminal justice services received by a patient during the preceding 6-months are recorded. It allows costing of services received after weighting with unit cost data (for more details about the instruments, see Table 1 in Reference Becker, Knapp and KnudsenBecker et al, 2000).
Table 1 Reliability testing for each instrument
| Instrument | Score distribution: mean & s.d. tests | Internal consistency | Test-retest reliabilityI | Systematic change: paired t-test | ||||
|---|---|---|---|---|---|---|---|---|
| α | α test | κ | κ test | ICC | ICC test | |||
| CAN | ||||||||
| items | * | |||||||
| sumscore | * | * | * | * | * | * | ||
| LQoLP | ||||||||
| scales | * | * | * | * | * | * | ||
| sumscore | * | * | * | * | * | * | ||
| IEQ | ||||||||
| scales | * | * | * | * | * | * | ||
| sumscore | * | * | * | * | * | * | ||
| VSSS | ||||||||
| items | * | * | ||||||
| scales | * | * | * | * | * | * | ||
| * | * | * | * | * | * | |||
Reliability protocol
To compare the results from the reliability analyses for the different instruments, a strict protocol was developed (Reference Schene, Koeter and van WijngaardenSchene et al, 1997) to ensure that all centres used the same procedure and options, and the same software, to test the reliability of instruments and to compare the reliability results of the different centres. The protocol covered the following aspects: definition of the specific reliability measures used; description of the statistical methods to assess these reliability coefficients; development of statistical programmes to make intercentre reliability comparisons; criteria for good reliability; criteria for pooling v. not pooling data; and the general format for the reliability analysis. In Table 1 the reliability estimates used are presented for all instruments. The justifications for these estimates for each instrument are given in the separate papers in this supplement.
Statistics
Reliability estimates
Cronbach's α was computed for each site, using the SPSS reliability module (SPSS 7.5 or higher). ICCs were computed using the SPSS general linear model variance components option with maximum likelihood estimation in SPSS. Patients were entered as random effects, and in case of pooled estimates, the centre was entered as fixed effects. Variance estimates were transformed into ICC estimates with corresponding standard errors using an Excel spreadsheet, inputting the between-patient and error components of variance and their variance-covariance matrix, the latter being used to obtain standard errors based on the delta technique (Reference DunnDunn, 1989). Unweighted κ estimates were computed using the SPSS module ‘crosstabs’, weighted κ using STATA version 5.0 (Statacorp, 1997). The standard error of measurement for a (sub-)scale is computed by substituting Cronbach's α for pxx in the formula for the (s.e.)m given earlier (for α) or directly from the error component of variance (for ICCs).
Inter-site comparisons
Tests for differences in α values between sites were performed using the Amsterdam α-testing program ALPHA.EXE (Reference WoutersWouters, 1998, based on Reference Feldt, Woodruff and SalihFeldt et al, 1987). Homogeneity of variance between sites was tested with Levene's statistic. For all scales and subscales, Fisher's Z transformation was applied to ICCs to enable approximate comparisons to be made between sites (Reference Donner and BullDonner & Bull, 1983). Differences between sites were tested for significance by the method of weighting (Reference Armitage and BerryArmitage & Berry, 1994) before transforming back to the ICC scale. The standard error of measurement was obtained from the ‘error’ component of variance.
Finally, a paired t-test on test-retest data was carried out in order to assess systematic changes from time 1 to time 2. For the separate items of the CAN, test-retest reliability and interrater reliability for each site were computed as pooled κ coefficients. For the separate items of the VSSS, weighted κ values were computed by site and summarised into bands.
Reliability criteria
For a psychological test, standards used for good reliability are often α≥ 0.80, ICC≥0.90 and κ≥0.70. The instruments in this study, however, are not psychological tests, like (for instance) a verbal intelligence test. The constructs they cover are more diffuse than in psychological tests and the boundaries with other constructs (such as unmet needs and quality of life) are less clear. As a consequence, the items constituting these (sub-)scales are more diverse and less closely related than would be the case in a strict, well-defined one-dimensional (sub-)scale. Taking these points into consideration, applying the ‘psychological test’ standards for good reliability to our instruments seems somewhat unrealistic. Landis & Koch (Reference Landis and Koch1977) give some benchmarks for reliability, with 0.81-1.0 termed ‘almost perfect’, 0.61-8.0 ‘substantial’ and 0.41-0.60 ‘moderate’. Shrout (Reference Shrout1998) suggests revision of these descriptions so that, for example, 0.81-1.0 would be ‘substantial’ and 0.61-0.80 would be ‘moderate’. However, taking account of the special nature of the data in this study, one can consider 0.5 to 0.7 as ‘moderate’, and 0.7 and over as ‘substantial’, and these descriptions have informed the discussion of the adequacy of the coefficients.
Pooled v. separate analysis
In a multi-site study such as this, there are many reasons why one might wish to combine data from the different sites: to summarise the reliability analyses, to identify comparable patients in different sites, and to obtain a larger sample for regression analyses. Whether combining data is reasonable depends on the aim of the analysis and on the results of the reliability analysis for each site.
A first aim is to summarise the level of reliability in the study as a whole. Computing a pooled estimate of a reliability coefficient is reasonable if the site-specific coefficients do not differ significantly. Otherwise a pooled estimate would obscure the variations - but, subject to this proviso, it might nevertheless provide a useful summary.
A second aim is to make comparisons between patients from different sites with the same scale scores: for example, in order to compare outcomes between sites adjusted for differences in symptom severity. This requires scale scores for symptom severity to have the same meaning in different sites. Unfortunately the reliability analysis is unable to tell us whether this is the case. Even with perfect reliability, site A might consistently rate the same actual severity higher than site B; yet this might not be apparent from the data if the mean severity was lower in site A.
A third aim of pooling the samples is to have a larger sample on which to conduct correlation or regression analyses. The possibility discussed above (that sites may differ systematically) makes it desirable that these analyses should adjust for site. Differences in reliability are also important in this case. Lack of reliability in outcome variables will decrease precision, and where this differs between sites, weighting might be necessary. For explanatory variables, there is the more serious problem of bias due to their unreliability, which again might differ between sites. These ‘untoward effects’ of inefficiency and bias are vanishingly small when reliability is moderate (Reference ShroutShrout, 1998), but one would nevertheless wish to ensure that apparent differences between sites were real, and not just due to these effects. A possible solution for the bias problem is to use ‘errors in variables’ regression, which can adjust for the effects of differing reliabilities at each site. Analyses should, strictly speaking, be carried out on the type of patients for whom reliability has been established. In the present study, the reliability study was nested within the large substantive study, and the inclusion criteria were similar across sites, so there should be no major problem here.
Analysis scheme
For all instruments the following analysis scheme is followed: assess the site-specific reliability estimates (α, ICC, (s.e.)m); test for inter-site differences in reliability estimates; test for inter-site differences in score distribution (mean and variance) (ANOVA, and Levene test).
In addition to the site-specific analyses, pooled reliability estimates are made. Where all estimates are high (say, above 0.9), then small differences in reliability between sites may be statistically significant, yet relatively unimportant in practical terms. However, where reliability is generally lower, or lower for one or more sites, differences in reliability between sites imply that pooled estimates should be treated with great caution. In such cases, it is necessary to extend the inter-site comparisons with a consideration of the site (s.e.)m values, differences in underlying score distributions, and possible reasons for differences: for example, in the way in which the instrument was applied. Furthermore, any imprecision and bias due to such differences would also need to be taken into account in the analysis of pooled data, in the ways mentioned above.
For the CSSRI a different approach was chosen, because the CSSRI-EU is a new instrument developed for use in a European setting. Since it is an inventory of socio-economic indicators and service variables rather than a multi-item rating scale, the focus is on achieving validity rather than formal reliability (for more details see Reference Chisholm, Knapp and KnudsenChisholm et al, 2000, this supplement).
CONCLUSION
Many technical issues surround the choice of measures of reliability. Such measures are tools which indicate, among other things, the degree to which associations between variables may be diluted; and poor realiability indicates a problem with an instrument when used to quantify associations. Although good reliability does not necessarily indicate a good instrument, reliability studies are one of the best means available to validate our translated instruments.
ACKNOWLEDGEMENTS
The following colleagues contributed to the EPSILON Study. Amsterdam: Dr Maarten Koeter, Karin Meijer, Dr. Marcel Monden, Professor Aart Schene, Madelon Sijsenaar, Bob van Wijngaarden; Copenhagen: Dr Helle Charlotte Knudsen, Dr Anni Larsen, Dr Klaus Martiny, Dr Carsten Schou, Dr Birgitte Welcher; London: Professor Thomas Becker, Dr Jennifer Beecham, Liz Brooks, Daniel Chisholm, Gwyn Griffiths, Julie Grove, Professor Martin Knapp, Dr Morven Leese, Paul McCrone, Sarah Padfield, Professor Graham Thornicroft, Ian R. White; Santander: Andrés Arriaga Arrizabalaga, Sara Herrera Castanedo, Dr Luis Gaite, Andrés Herran, Modesto Perez Retuerto, Professor José Luis Vázquez-Barquero, Elena Vázquez-Bourgon; Verona: Dr Francesco Amaddeo, Dr Giulia Bisoffi, Dr Doriana Cristofalo, Dr Rosa Dall'Agnola, Dr Antonio Lasalvia, Dr Mirella Ruggeri, Professor Michele Tansella.
This study was supported by the European Commission BIOMED-2 Programme (Contract BMH4-CT95-1151). We would also like to acknowledge the sustained and valuable assistance of the users, carers and the clinical staff of the services in the five study sites. In Amsterdam, the EPSILON Study was partly supported by a grant from the Nationaal Fonds Geestelijke Volksgezondheid and a grant from the Netherlands Organization for Scientific Research (940-32-007). In Santander the EPSILON Study was partly supported by the Spanish Institute of Health (FIS) (FIS Exp. No. 97/1240). In Verona, additional funding for studying patterns of care and costs of a cohort of patients with schizophrenia were provided by the Regione del Veneto, Giunta Regionale, Ricerca Sanitaria Finalizzata, Venezia, Italia (Grant No. 723/01/96 to Professor M. Tansella).
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