THE SIN OF SUBJECTIVISM: GEORGE W. BROWS
A REPLY
TO SHAPIRO
and TIRRIL HARRIS
Department of Sociology, Bedford College. Regent’s Park. London N.W.I.. U.K (Rewired 30 April 1979)
Summary-Shapiro criticises our book on two grounds. He first outlines a series of mistakes. None of them we believe. in fact. have been made and this is usually quite clear from our book. His second criticism rejects our ‘subjectivist‘ approach to measurement. We argue that he misrepresents our methods and fails to grasp their ability both to collect accurate data and deal adequately with possible sources of bias. Indeed in these, in its attention to the dating of both independent and dependent variables. and in the flexibility of its approach to the respondent. we feel our approach is better equipped than other existing instruments to tackle the problem of the aetiological role of psycho-social factors in illness.
Shapiro accuses us, at least in the first six chapters of Social Origins of Depression which is all he has read, of ‘relative subjectivism’. In doing this he links two rather different shortcomings by the same pejorative term ‘subjectivism’. On the one hand he disapproves of our overall approach to measurement; on the other he picks out a number of things which he considers to be mistakes introducing bias in our work-bias so fatal that it rules out any need to read the last eight chapters of the book. He sees both shortcomings as related: for he claims that the relative subjectivist “will therefore focus his investigations of his (own) judgements and not look critically at the way he collects and analyses his data” (p. 5). The topic of our approach to measurement should be the main issue discussed in this reply since it appears peculiarly difficult for psychologists to accept, and it is a rare opportunity for us to expound it in the pages of a psychologists’ journal. But before we do this we should deal with Shapiro’s other ‘subjectivities’ which he implies are an inevitable result of our general approach. We should say at once that we have been puzzled by them. We have reread the relevant parts of our book and find that in almost every instance the text itself shows that we have not made the mistakes or omissions he claims. We shall try to deal with his chronicle of our shortcomings in the order he lists them: (1)
ANALYSIS
OF
RESULTS
Shapiro picks three of our analyses which cause him distaste. They all involve severe events which are the only type of life-event that we found capable of bringing about clinical depression. The first two concern their distribution before onset of depression (an average period of nine months). For this he demands “the provision of measures of central tendency and dispersion”. In this he ignores a special characteristic of our data which would make such presentations dificult-that the time period covered for the patients varied between 13 and 50 weeks. And he fails to make clear what difference knowledge of these measures could make to the argument we present. In our book we conclude that it is just one severe life-event that is in most instances critical in bringing about depression and that there is a very large difference between patients and those without depression in the proportion having at least one such event. For this conclusion the data we present are entirely adequate. We start by giving rates of various types of events (to which Shapiro objects); we then give the proportions experiencing at least one severe event; then give the proportions with at least one, two and three or more severe events (p. 108) and finally we demonstrate that experiencing more than one severe event does little or nothing to increase risk of depression compared with experiencing only one (Shapiro ignores the last two analyses). We reject his implication that there has been some kind of scientific fraud. And what does he mean by his comment that the difference
HR.7,7&r
605
in the proportlon of depressed and other bvomen having at least one severe sbsnt “is salid be significant”‘? The difference in proportions is high!! significant and if he has reason to doubt our claim hz should state his reasons. In discussing our third ‘mistake’ he has misunderstood the text and indeed the logic on which the whole approach to the study of the aetiological role of life-events is based. He questions our claim that the role of severe events is unlikely to have been intluenced by problems of recall. He thinks that in makin, 0 this claim we ha\.e ignored our obvn data because for the depressed purirr~ts our graph shows a large drop in the number of severe events reported as occurring more than nine weeks before onset. In fact. of course, we never argued the conclusion about recall from the rate of events for patients. but from the rates for women in Camberwell without depression over the I6 3-Lveek periods before interview. If life-events are of aetiological significance then one would expect the patients’ events to show clustering around the time of onset at a much higher rate than earlier in the year; this would be a sign not of a fall-off in the recall by patients of events further away in time but of the fact that they had actually experienced many more events in the pre-onset period. The patients have a higher rate in this period just because there IS a causal link between severe events and their depression. It would therefore be nonsense to LISA’a-patient group to investigate the fall-off in recall over time. Such an investigation only makes sense in a group such as a random selection of the general population where there is no other reason to expect a difference in the actual occurrence of events at different times. The graph pertainin, 0 to ‘normal’ women (Brobvn and Harris. 197Sa: 102) makes it clear that our claims are perfectly consistent Lvith our data: the rate of severe events for these women does not fall off as one moves further back in time from the data of interview. to
(2) SELECTION
OF
SUBJECTS
Shapiro is quite right to emphasise the importance of recruiting subjects into an investigation in such a way as to maximise the independence of the two main groups of variables. We were very aware of this and regret that we appear not to have made this clear in our text. Perhaps this is because we omitted to discuss the letters sent to interviewees describing the project for them; but perhaps Shapiro overlooked or misunderstood bvhat we did say, so that it may be worth outlining our selection procedures again. (a) Patier1ts
The criteria for selecting patients were more or less what Shapiro Lvould wish when he writes “a series of patients in exact order of admission kvho were diagnosed by clinically responsible psychiatrists who had nothin, 0 to do with the project” (p. 9). For the inpatient series the names of patients were obtained by weekly scrutiny of hospital records kept on the wards; and for out-patients ‘outside’ psychiatrists were contacted regularly by telephone to ask for the names of all those in their current out-patient sessions whom they had diagnosed as depressed. However, as we explain (op. cif. p. 51) some patients with primary depression might be excluded from the project (and this is why we say our selection was ‘more or less’ rather than ‘exactly’ what Shapiro would wish). There were only two grounds for such exclusions: first if the clinical picture was complicated by an underlying condition such as alcoholism or organic psychosis, and second if there had been no change in the patient’s state for twelve months or more. The latter condition was an obvious necessity, for, if we sought to examine the role of life-events and ditficulties in the onset of depressive disorders, we would have to examine their occurrence in a period which predated the disorder. Since both grounds for exclusion related to the dependent variable, they are unlikely to have introduced any bias into the results. It was only after we had selected women in these ways th’at Dr. Copeland, the research psychiatrist involved with the project, interviewed them. Patients were told that the research was about about the onset of the depression and would involve answerin, 0 al! sorts of questions themselves (no more no less). Relatives were told much the same. The co-operation
The sin of subjecflvism:
A reply to Shapiro
607
shown by the patients and their relatives was excellent. Of those included as clinically suitable on the two grounds mentioned above. not one refused to participate.
Shapiro correctly reports that we first selected households at random and then, also at random. the one woman per household to be interviewed. We chose this method because if we had selected from lists of individuals such as electoral registers. or lists of women registered with general practitioners, we might well have missed just those people with a recent move into the area who had not yet had time to register on these lists; in fact there might then have been a bias which would reduce the rate of life-events like residence changes in our comparison group. It is exactly a measure of our awareness of such a bias which underlay our particular sampling design (Brown and Harris, 197Sb). The women in the community sample were asked to participate in a survey about the health of women and their families in this area’. No mention was made of psychiatric health. depression or ‘life-events’ in the introductory explanation. It was explained to them that their house, rather than their name, had been selected at random, and quite often the interview was completed without the interviewer discovering the woman’s name. although most were quite happy to give it. The interviewers were highly motivated to minimise the refusal rate, and would spend many minutes on the doorstep persuading people that just because they had no health problems it did not mean that there was no point in interviewing them. One woman was visited some 15 times before she finally agreed to participate (the other fourteen times she kept giving plausible reasons why she could not be interviewed on that particular day). The percentage of refusals was 170/h which, given the nature and length of the interview, compares favourably with other surveys. Our worry was that women in the community who had recently experienced severe events might be less willing to be interviewed, thus artificially lowering the rate of events in the comparison group. But to assume that such women are ‘normal’ rather than cases of depression is quite a conservative assumption, and perhaps more likely is that those refusing are more depressed than those agreeing. Subsequent consultation of the Camberwell case-register gave some hint of this for the second series of women seen in Camberwell. (Unfortunately it was not possible to do this check for the first series). However, with a refusal rate of only 17x, such biases, even if they did affect our data. would hardly overturn the direction of our results. (3) CASES
IN
THE
COMMUNITY: WITH
DEPRESSED
HOW
COMPARABLE
ARE
THEY
PATIENTS’?
Shapiro seems to have been confused by our five-point severity scale at this point. He argues that because only I 1% of our cases are on the top two points of this scale they are therefore likely to be ‘normal’ women undergoing ‘signs of stress’. He fails to see that the same conclusion must logically apply to the 56% of the depressed out-patients who were rated on the bottom three points of the severity scale. The crucial threshold is clearly not between the top two and the bottom three of these five points but between the fifth point and the category of reactions which we labelled ‘borderline cases’ and included in the ‘normal’ group of women for purposes of our analysis. This threshold, between ‘case’ and ‘borderline case’, when examined later after the publication of the Feighner criteria for depression, was surprisingly similar to that of Feighner and his colleagues (cf. Brown and Harris, 197Sa. pp. X3-59; Feighner et al., 1972). Shapiro is worried that by excluding these ‘stress reactions’ from our comparison group we have artificially lowered the rate of severe events in this group. It might reassure him to know that in assessing the importance of life-events in bringing about depression we used a measure of association which takes account of the chance juxtaposition of event and disorder and that the wlzole general population including both ‘cases’ and ‘normals’ was used to calculate the base rate of severe events in the formula (op. cit. Chapter 7, pp. 117-121). (As will be seen there are other reasons why it is unfortunate that Shapiro did not read Chapters 7-14 of our book.)
603
GEORGE W
BROW
and TIRRIL HARRIS
Shapiro refers to Tennant and Bebbington’s paper reviewing our book in connection with this issue of caseness but not to our reply (Brown and Harris. 1978b; Tennant and Bebbington. 1978). Perhaps he decided not to bother to read that too. We do not have space here to repeat the many points made in that reply. but it should be stressed that our measure of caseness is much stricter than those used in most recent population studies of psychiatric disorder (see also Finlay-Jones and Murphy. 1979). The real problem which bedevils this issue is that no-one has yet developed criteria other than the two we use (severity and duration) which can be used objectively (sic) to distinguish stress reactions from clinical depression. We should however state at the outset that many authors who discuss transient stress reactions are dealing with wry transient ones, lasting a week or less. For example Duncan-Jones and Henderson (1978) described how in research using a two-stage design, first screening with the GHQ and then giving a PSE later, there were often discrepancies between the responses on the two by the same person, especially if more than a week elapsed between the stages. Our cases were required to have experienced a minimum duration of symptoms of lOdays. regardless of the intensity. In practice the shortest ‘episode’ we recorded among the cases was four weeks. The interviewers supplemented the shortened version of the PSE with a number of questions about the course and fluctuation of symptoms, but since the majority of cases had not recovered during the year before interview this information only gives us assurance about the minimum duration of episodes, not about their overall duration. Only detailed follow-up studies tracing the course of episodes until the point of recovery, and comparing community cases with psychiatric outpatients, will clarify whether there is any more than faith to support the notion of the difference between a distress reaction of a certain severity and of minimum duration and a ‘real’ depression. We suspect if a criterion ever does emerge it will relate to some feature of personality organisation, the measurement of which will be very complicated. In the meantime progress can only come from sorting subjects as we have done into groups of comparable symptom severities. One final point on this topic: Shapiro says that it would be worthwhile comparing event scores of each of the various sub-groups. At different points in the book we do in fact do this (e.g. Chapter 12 looks at ‘borderline cases’ separately from the other women and Chapter 13 compares in-patients and out-patients). (1)
THE
MEASUREMENT
OF
LIFE-EVENTS
(a) Validitj Shapiro is unwilling to accept our patient-relative agreement study as a form of validation. While it is, of course, true that family folk-lore may exist about events this does not imply that such a study is meaningless in terms of validity. It is in any case inconceivable that a complete check on validity could be done without interviewing others who knew the person. Only a minority of events have some kind of public record and in using records of say deaths, marriages, births and hospital admissions as checks on validity it is infinitely easier to locate ‘false positives’ (e.g. a death reported by the subject but not recorded officially) than it is ‘false negatives’ (e.g. to find about ‘missing’ deaths one would not only have to run through all registered deaths in the country but also check their attachments to the person concerned). Since our research grants did not run to the latter monumental undertaking we confined our formal test of validity to a patient-relative agreement study (which allows the checking of both false negatives and false positives). In this comparison we found for severe events (i.e. those of causal importance) a 91% agreement between patient and relative about the occurrence of specific events. We believe we had every justification to be impressed by this result and that it represents an important test of the instrument’s validity. The level of agreement may however appear less surprising when it is’ remembered that severe events represent incidents of considerable importance such as a husband leaving home, death of a parent. birth of a baby and life-threatening illness of someone close. The importance of these events also explains why we were not concerned with bias from ‘family folk-lore’. We find
The sin of subjectlvism:
A repI> to Shapiro
605,
it difficult to believe that the events had not in fact occurred. What influence therefore could reasonably be expected from such folk-lore? The only possibility that occurs to us is that in some way the date of the event could be confused. Here we made an effort in the earlier study of schizophrenia (Brown and Birley, 1968) as well as in the work on depression to check the dates of important events with ‘public records’. This extremely rarely led to a change in the time ordering of the event and onset. If any systematic bias for events to be dated before rather than after onset has crept into our results, there are however implications which Shapiro does not follow through in his critique; for there would then be a much higher rate of severe events after onset among the depressed than among the normal women which would require elucidation. The only reasonable explanation for this would then be that the depressive disorders had somehow brought about the severe events. Since we had used a measure of the ‘independence’ of events (their independence that is of the behaviour of the respondent) we could examine this alternative notion: how feasible is it to say that the high rate of severe events could really be due to the respondent’s activities under the influence of depression, and that biased reporting had placed them incorrectly before rather than after onset? On pp. 103 and 347 we give figures which show that depressed women experiencing severe events which were on logical grounds likely to be largely ‘independent’ of their volition were more than four times more common than those experiencing only severe events which may somehow have been brought about by their own actions. When considered separately both types of severe event showed the same order of association with onset of depression. It makes no sense to suggest that, say, a letter from the Council notifying one of the imminent demolition of what has been one’s home since childhood (an obviously ‘independent’ event) could happen more frequently in a group of women just because they were already depressed. Shapiro ignores our measure of ‘independence’, but we feel that our results on this dimension clearly support the conclusion that no really important bias has crept in to our dating of events and onsets. (b) Dimerisiorrs of‘/ife-ecetits Shapiro complains that the scales describing events are not presented in full. He must have missed pp. 95-97 of our book where they are given in full to describe two events in detail. He says we do not give details of the reliability of the threat rating but in fact we do in a footnote to Chapter 5, p. 346. Shapiro says we do not make explicit the criteria for the ratings. In fact the whole chapter on ‘Meaning’ does so in general terms; of course to do so more specifically in the sense of enabling someone to repeat our ratings, would have involved a lengthy discussion devoted to each different type of event probably taking well over one hundred pages of text. This was clearly inappropriate in our book. However, we do have both a Dictionary of Threat Ratings and a Training Handbook if anyone needs the detailed criteria, and we provide these to interviewers who wish to train in our methods. (We have now successfully trained more than a score of other workers in these ratings.) We should perhaps also mention a paper by Tennant et al. (1979) which reports a reliability study of ratings of severity of the contextural threat of events made during our team rating meetings. This concludes that the ratings can be made with very satisfactory reliability. Having dealt with the chronicle of our ‘mistakes’ it will be clear that we have been just as concerned with the possibility of bias as Shapiro himself. His suggestion that as ‘relative subjectivists’ we do not look critically at the way we collect and analyse data is false. It is precisely because we have been so concerned that we have measured things in the way we have; for we see a great distinction between the demand to minimise bias, which we accept as essential in scientific research, and the need to minimise subjective judgements by investigators. The first does not require the second. So long as judgements by investigators can be made reliably there is nothing necessarily wrong with using definitional criteria to which the subjects of the study are not party. Since there is no dispute about the need for reliability we will start with Shapiro’s use of the term ‘subjectivity’. One meaning is linked to the idea of reliability: when criteria
610
GE~RCE W. BROW* and TIRRIL HARRIS
are private there can be no guarantee of reliability. that is comparable and repeatable use of descriptive categories. One just has to trust that when the person talks of. say anxiet) states, on one day he is using the same criteria as he used on another. In this sense our study was not subjective. Our criteria for ratin g were almost tediously public. We spent much time developing criteria defining the boundaries of our categories such as events and their dimensions which were then embodied in a manual and no interviews were included in the survey until the interviewer had undergone a lengthy training in their use. Critical ratings such as those concerning the threat of events or psychiatric ‘caseness’ were always brought to weekly rating meetings and re-rated by the whole research team (without prior knowledge of the interviewer’s rating.) This procedure even on the most complex ratings produced high reliability standards which bvere public and shared.* Another meaning of subjective is that, despite being public and shared. the standards are still not shared by everyone: they are only shared by a group of individuals. In this sense our work is ‘subjective’; and for this we make no apology. It had to be by the very nature of the project we were investigating. Different people define in different Lvays what is and what is not stressful: what is and what is not depression. There never will be a miwrsaIly acceptable set of public criteria. Under such circumstances there are three possibilities open to an investigator: one is to take the subjectivity of his respondent as his defining principle-anything defined by the respondent as stressful he will accept as stressful, anything defined by the respondent as depression he will accept as depression. A second course is for the investigator to apply standards of his own, and to make these public and repeatable. And a third is to give up all hope of investigating the area because of the lack of objectivity. Shapiro berates us for choosing the second course. but there are so many pitfalls attendant on the first that if he cannot find it in him to accept the second course the only option he has left is the third, to give up any attempt to study this topic in causal terms. But just before we outline the pitfalls of the first approach, it is worth saying that when we chose the second approach as the main basis of our analysis we did not shun the first completely. The team assessment of the conte.stual threat of events was based rlor on our estimate of how \t’e would react to an event of particular kind, but on how we thought the majority of people in similar biographical circumstances would react to it. We were not therefore using our own reaction to the event but our judgement of how most women would feel about it in the circumstances. While the latter procedure is, of course, subjective, it is not so in quite the same way as the former would be. It should also be noted that in making such contextual ratings the team of raters were not told how the woman said she had responded to the event. It was essential to do this in order to rule out important possible sources of bias. If we had allowed such self-reports to influence the contextual threat ratings we could never have hoped to rule out the dangers attendant on the first of the three strategies. We have devoted much attention in one of the chapters read by Shapiro to the pitfalls of choosing the respondents’ rather than the investigators’ definitions. We maintain that this can introduce not merely random errors, but a systematic bias either of ‘direct contamination’, ‘indirect contamination’ or ‘spuriousness’ (op. cit. pp. 73-81). As a quick example of one of these, consider the possibility that the more anxious, despite having exactly similar experiences to their less anxious counterparts. may see life-events such as illnesses of a close relative as more stressful and report them more often in answer to general questions about illnesses in the family. But, if it is their anxiety and not the events they report that gives rise to their depressive disorder. the association between events and depression would be spurious. not causal. We can be confident that our data is not contaminated in this way because we guarded against this bias both at the stage of interviewing and of rating. At interview we did not ask what had been found upsetting but only about the occurrence of certain events irrespective of the respondent’s reactions to them; we were careful to probe in a way that facilitated the remembering of events by * L+‘rbelievr that the term O~/YCII~.CIS best used to describe reliable measures. ment between Independent ratrrs IS a particularly important form of rrllability: ‘intersubjectivity’ (Galtung. 1967, pp. JS-29).
For soaologlsts what Galtung
the agreehas called
The sin of subjectlwsm:
A reply to Shapiro
61 I
people whose less anxious personalities might have gone with a tendency to give less prominence to anxiety-arousing experiences, with a consequent tendency to recall them less readily than their more anxious neighbours. When it came to the stage of rating the tape-recorded information the many rules for inclusion or exclusion of events ensured that the same standards were applied to both the anxious and the less anxious respondent: thus many of the illnesses mentioned by the more anxious subject would not meet the criteria for inclusion on the rating schedule. Furthermore. as we have already emphasised. once the details of an event had been collected we ignored the woman’s reported reactions to it in rating contextual threat. Shapiro is quite right to point out that the PSE is like the life-events interview in exactly these ways. This is why we chose it. A semi-structured interview with probes, it takes the interviewing team’s definition, for example. of ‘delayed sleep’ as the criterion for a positive rating, not the respondent’s definition. For with symptoms as with life-events there may be systematic reporting biases. For example, a more highly defended person may say they have not really been all that depressed and another person say that they have ‘really been feeling dreadful’, but it is only on probing that it emerges that the second person can always be cheered up when someone else comes in whereas the first has often sat in company trying to participate and feeling low throughout. (The more defended person may also be less anxious and so recall life-events less readily without extra reminders.) There is a long and respectable tradition in psychology which tries to correct for ‘response-sets’ and which acknowledges such reporting biases. But there is also a tradition which encourages the use of paper and pencil questionnaires, a feeling that they are somehow safe, sterilised from the interviewer biases which are an inevitable part of face-to-face interviews. The sins of interviewer bias are considered at the expense of noticing respondent bias. Although Shapiro does not devote much space to it we suspect that what underlies all his other criticisms is his worry that our work may be subject to interviewer-bias through halo-effects. Of course it is quite true that the same interviewer collected both life-event and symptom data in the general population and out-patient samples, and that such a procedure could lead to differences both at the stage of data collection and of rating in the way ‘cases’ and ‘normals’ were treated. For example. a woman with obvious depressive symptoms might be more closely questioned for events, or there might be a tendency to rate her events as more severe than those of a normal woman. One way of controlling for the latter (at the stage of rating) is our procedure of team rating meetings where the events are presented to raters who are blind to knowledge of the woman’s symptoms, and vice versa. A way of controlling for the former (at the stage of questioning the woman) is to ensure that the interviewers are trained properly in unbiased interviewing. This involves establishing an ethos in which interviewers are taught almost to be biased in the opposite direction from the hypothesis which they cannot fail to know they are helping to test. Our interviewers were taught to keep on probing for life-events with ‘normal’ respondents if anything longer than with ‘cases’. Conservatism (in terms of the hypotheses to be tested) was also the guiding principle at the stage of rating if ever there were uncertainties in deciding for example between marked and moderate long-term contextual threat; (for we are not pretending that such uncertainties never arose-life is fortunately more varied and idiosyncratic than the specifications of our training manual, and new standards had to be created from time to time.) Under such circumstances events occurring to patients were nearly always rated down (as less threatening) on principle (for greater detail about this cf. op. cit. pp. 147-149). Finally in assessing the likely degree of bias in our work there is a further form of validity to which psychologists have given a good deal of attention and which Shapiro entirely ignores; this is ‘construct validity’. It is an interesting form of validity because it depends on the relationship of actual results of the research to predictions made either on logical or theoretical grounds about them. There is an element of ‘the proof of the pudding is in the eating’ about this approach and as with puddings it can take many
hi’
GEORGE W. BROW\ md TIRRIL H,ARRIS
forms. Thus in our own work we place considerable importance on the fact that although severe events form only 169, of all the events occurring to women in Camberwell. it was only these severe events that played a formative causal role. a result repeated in three separate studies (op. cit. Chapter 7). The logical point is that if there had been significant bias stemming either from the interviewer or respondent one would not have expected the association to occur only for one fairly infrequent type of event but to have applied also to other events. Furthermore. events severely threatening only in the short-term (a child nearly dying but recovering within a week) showed no association whatsoever with onset of depression. We are convinced that these results were in no way anticipated by the raters and it is hardly convincing to argue that our respondents themselves made such distinctions. Probably as great a danger facin g any academic discipline as that of bias and error in its measures is the turning of a once effective technique into ritual. The sense of safety which the use of a well established pencil and paper fired-choice questionnaire can bring is an example of just such a ritual. The streamlined procedure lends speed to the analysis of the data and discourages potential critics like the label from a prank--cru vineyard. But this does not mean that other wines cannot have their own particular value. Face-toface interviewing allows so many things which can enhance validity if interviewer biases are properly controlled-for example difficult words can be defined for the respondent’s benefit. All too often a respondent will say “well that depends”. and it can be of great importance on what it depends, in which situations that personality item is true of him and in which it is not. Paper and pencil questionnaires cannot usually provide enough alternatives to account for all these situations straightforwardly, while verbal interviews can usually resolve the matter. The interest in situationally specific measures of personality over recent years suggests that psychologists are now beginning to reaiise how much valuable information can be missed by generalised questions (Mischel, 1968). It is a pity that these moves tend to be seen in terms of new theoretical perspectives rather than as a means of circumventing totally inadequate methods of measurement. The use of tones of voice can be of crucial importance in measuring certain features of the home environment which are significantly related to relapse in schizophrenia [cf. Brown, Birley and Wing (1972) and Vaughn and Leff (I 976); for detailed discussion of the development of these measures cf. Brown and Rutter (1966) and Rutter and Brown, (1966)]. The creative way to confront these areas is to develop methods of measurement which capitalise on the advantages of face-to-face interviewing while imposing maximum control on interviewer bias, not to retreat into the time-honoured instruments which can miss the crucial dimensions concerned. There is an obvious danger in replying to such provocative criticism that one may seem arrogant in one’s own defense. Having emphasized the advantages of our ‘subjectivist’ approach and stressed the efforts we took to minimise bias, we have no wish to convey the impression that no improvements could be made in our work. The study was naturally subject to the restrictions imposed by time and money. and doubly so because it was largely pioneering; life-event research had not been done in this way before in Britain. Now that its feasibility is accepted we have been fortunate enough to obtain further funds for a prospective study in which some of these improvements can be made. The obvious advantage of a longitudinal study over a cross-sectional one is the greater certainty in ruling out the reporting biases which experience of a depressive episode may introduce into the recall of retrospective data. (As we have already conveyed we do not believe that important bias is likely for the life-event material but it certainly is a possibility for some of our ‘softer’ measures such as intimacy.) It will be possible in this much larger study to introduce checks and refinements not possible in a study without follow-up interviews-for example, if a respondent has initially agreed to participate with several interviews it will be possible for two different interviewers to be used, one asking only about life-events without any questions about symptoms. A small sub-study comparing the results of this interview with those of the main interviews would provide further surety on halo-effects and interviewer bias. Follow-up too should allow a much
6 1;
The sin of SubJectivlsm: .A rep{? to Shapuo
more subtle approach to the caseness-borderlineness threshold. As in earlier research with schizophrenia it is necessary to move in this way from cross-sectional to prospective designs (see Brown, Birley and Wing. 1972). In the end scientific advance usually comes from the convergence of many different lines of evidence; from several methods of approach rather than from a ‘definite experiment’ which is beyond reproach. Sin in measurement is not in Shapiro’s subjectivity but in the belief that it is necessary to find methods that are beyond all reproach-it is a sin because it leads either to hopelessness about what can be done or to blind faith in a limited technique. We are convinced that a truly effective and creative social science must be built round the kind of empathic measurement discussed by Max Weber and others in terms of rersrel~en and which we have attempted to develop. Our confidence in our results stems from the flexibility of this approach and its ability to use the most sensitive of all measuring instruments-the human mind. Shapiro’s view therefore both of our errors and of our philosophy of measurement is inaccurate; we hope that this reply will be enough to convince readers to look further at our book and judge for themselves the merits of our methods. ~cl;,lo~~l~dgrnrrrIt-Ws Register.
are grateful
to Jane Hurry
for her help in the use of the
Camberwell
Psychiatric
REFERENCES Brows G. W. and RUTTERM. (1966) The measurement of pamily activities and relationships: A methodological study. Huv~nn Rel. 19. 241-763. BKO~VU G. W.. BIRLI:\I’ J L. T. and WING J. K. (1972) Influence of family life on the course of schizophrenic disorders: a replication. Br. J. P.s.rcltiaf. 121. 1-i-25s. BROWN G. W. and HARHIS T. (I978a) Social Orlgirrs o/ Drprrssiopt. Tavistock, London. BROWS G. W and HARRIST. (1978b) Social Origins of Drprrss~on: a reply. Psycho/. Mrd. 8. j77-5YY. BROWS G. W. and BIKLEYJ. L. T. (1968) Crises and hfe changes and the onset of schizophrenia. J. Healrl! sot. Brh. 9, 203-214. DL~CAS-JOS’ES P. and HESDEKSONS. (1978) The use of a two-phase design in a prevalence survey. Sot. PS)C/IiUf. 13, 23 l-737. FINLAY-JONFS R. A. and ML’KPHY E. (1979) Severity of psychiatric disorder and the 30-item General Health Questlonnalre. Br. J. Pvycl~ic~r. 134. 609-616. GALTUSG J. (1967) Theory nrld Mrrhods o/~Sociul Research. Allen and Unwon. London. MISCHEL W. (1968) Prrsorul~ry and Assessment. John Wiley, New York. RC’TTVR M. and BKOWN G. W. (1966) The reliability and validity of measures of family life and relationships in famllies containing a psychiatric patient. Sot. Psychor. 1. X-53. TES\A\IT C. and BEBHI~GTOX P. (1975) The social causation of depression: a critique of the work of Brown and his colleagues. Ps~cl~ol. hlrd. 8, 565-575, TI SUST C.. SMITH A.. BEHNSGTON P. and HURKI, J. (1979) The contextual threat of life-events: the concept and its rcliabillty. Ps~.ho/. .\fvc/. (in press). VAUGHS C. and LEFF J. (1976) The intluence of family and social factors on the course of psychiatric illness: a comparison of schizophrenic and depressed neurotic patients. Br. J. Psychiur. 129, 125-137.
A REPLY
TO SHAPIRO
and TIRRIL HARRIS
Department of Sociology, Bedford College. Regent’s Park. London N.W.I.. U.K (Rewired 30 April 1979)
Summary-Shapiro criticises our book on two grounds. He first outlines a series of mistakes. None of them we believe. in fact. have been made and this is usually quite clear from our book. His second criticism rejects our ‘subjectivist‘ approach to measurement. We argue that he misrepresents our methods and fails to grasp their ability both to collect accurate data and deal adequately with possible sources of bias. Indeed in these, in its attention to the dating of both independent and dependent variables. and in the flexibility of its approach to the respondent. we feel our approach is better equipped than other existing instruments to tackle the problem of the aetiological role of psycho-social factors in illness.
Shapiro accuses us, at least in the first six chapters of Social Origins of Depression which is all he has read, of ‘relative subjectivism’. In doing this he links two rather different shortcomings by the same pejorative term ‘subjectivism’. On the one hand he disapproves of our overall approach to measurement; on the other he picks out a number of things which he considers to be mistakes introducing bias in our work-bias so fatal that it rules out any need to read the last eight chapters of the book. He sees both shortcomings as related: for he claims that the relative subjectivist “will therefore focus his investigations of his (own) judgements and not look critically at the way he collects and analyses his data” (p. 5). The topic of our approach to measurement should be the main issue discussed in this reply since it appears peculiarly difficult for psychologists to accept, and it is a rare opportunity for us to expound it in the pages of a psychologists’ journal. But before we do this we should deal with Shapiro’s other ‘subjectivities’ which he implies are an inevitable result of our general approach. We should say at once that we have been puzzled by them. We have reread the relevant parts of our book and find that in almost every instance the text itself shows that we have not made the mistakes or omissions he claims. We shall try to deal with his chronicle of our shortcomings in the order he lists them: (1)
ANALYSIS
OF
RESULTS
Shapiro picks three of our analyses which cause him distaste. They all involve severe events which are the only type of life-event that we found capable of bringing about clinical depression. The first two concern their distribution before onset of depression (an average period of nine months). For this he demands “the provision of measures of central tendency and dispersion”. In this he ignores a special characteristic of our data which would make such presentations dificult-that the time period covered for the patients varied between 13 and 50 weeks. And he fails to make clear what difference knowledge of these measures could make to the argument we present. In our book we conclude that it is just one severe life-event that is in most instances critical in bringing about depression and that there is a very large difference between patients and those without depression in the proportion having at least one such event. For this conclusion the data we present are entirely adequate. We start by giving rates of various types of events (to which Shapiro objects); we then give the proportions experiencing at least one severe event; then give the proportions with at least one, two and three or more severe events (p. 108) and finally we demonstrate that experiencing more than one severe event does little or nothing to increase risk of depression compared with experiencing only one (Shapiro ignores the last two analyses). We reject his implication that there has been some kind of scientific fraud. And what does he mean by his comment that the difference
HR.7,7&r
605
in the proportlon of depressed and other bvomen having at least one severe sbsnt “is salid be significant”‘? The difference in proportions is high!! significant and if he has reason to doubt our claim hz should state his reasons. In discussing our third ‘mistake’ he has misunderstood the text and indeed the logic on which the whole approach to the study of the aetiological role of life-events is based. He questions our claim that the role of severe events is unlikely to have been intluenced by problems of recall. He thinks that in makin, 0 this claim we ha\.e ignored our obvn data because for the depressed purirr~ts our graph shows a large drop in the number of severe events reported as occurring more than nine weeks before onset. In fact. of course, we never argued the conclusion about recall from the rate of events for patients. but from the rates for women in Camberwell without depression over the I6 3-Lveek periods before interview. If life-events are of aetiological significance then one would expect the patients’ events to show clustering around the time of onset at a much higher rate than earlier in the year; this would be a sign not of a fall-off in the recall by patients of events further away in time but of the fact that they had actually experienced many more events in the pre-onset period. The patients have a higher rate in this period just because there IS a causal link between severe events and their depression. It would therefore be nonsense to LISA’a-patient group to investigate the fall-off in recall over time. Such an investigation only makes sense in a group such as a random selection of the general population where there is no other reason to expect a difference in the actual occurrence of events at different times. The graph pertainin, 0 to ‘normal’ women (Brobvn and Harris. 197Sa: 102) makes it clear that our claims are perfectly consistent Lvith our data: the rate of severe events for these women does not fall off as one moves further back in time from the data of interview. to
(2) SELECTION
OF
SUBJECTS
Shapiro is quite right to emphasise the importance of recruiting subjects into an investigation in such a way as to maximise the independence of the two main groups of variables. We were very aware of this and regret that we appear not to have made this clear in our text. Perhaps this is because we omitted to discuss the letters sent to interviewees describing the project for them; but perhaps Shapiro overlooked or misunderstood bvhat we did say, so that it may be worth outlining our selection procedures again. (a) Patier1ts
The criteria for selecting patients were more or less what Shapiro Lvould wish when he writes “a series of patients in exact order of admission kvho were diagnosed by clinically responsible psychiatrists who had nothin, 0 to do with the project” (p. 9). For the inpatient series the names of patients were obtained by weekly scrutiny of hospital records kept on the wards; and for out-patients ‘outside’ psychiatrists were contacted regularly by telephone to ask for the names of all those in their current out-patient sessions whom they had diagnosed as depressed. However, as we explain (op. cif. p. 51) some patients with primary depression might be excluded from the project (and this is why we say our selection was ‘more or less’ rather than ‘exactly’ what Shapiro would wish). There were only two grounds for such exclusions: first if the clinical picture was complicated by an underlying condition such as alcoholism or organic psychosis, and second if there had been no change in the patient’s state for twelve months or more. The latter condition was an obvious necessity, for, if we sought to examine the role of life-events and ditficulties in the onset of depressive disorders, we would have to examine their occurrence in a period which predated the disorder. Since both grounds for exclusion related to the dependent variable, they are unlikely to have introduced any bias into the results. It was only after we had selected women in these ways th’at Dr. Copeland, the research psychiatrist involved with the project, interviewed them. Patients were told that the research was about about the onset of the depression and would involve answerin, 0 al! sorts of questions themselves (no more no less). Relatives were told much the same. The co-operation
The sin of subjecflvism:
A reply to Shapiro
607
shown by the patients and their relatives was excellent. Of those included as clinically suitable on the two grounds mentioned above. not one refused to participate.
Shapiro correctly reports that we first selected households at random and then, also at random. the one woman per household to be interviewed. We chose this method because if we had selected from lists of individuals such as electoral registers. or lists of women registered with general practitioners, we might well have missed just those people with a recent move into the area who had not yet had time to register on these lists; in fact there might then have been a bias which would reduce the rate of life-events like residence changes in our comparison group. It is exactly a measure of our awareness of such a bias which underlay our particular sampling design (Brown and Harris, 197Sb). The women in the community sample were asked to participate in a survey about the health of women and their families in this area’. No mention was made of psychiatric health. depression or ‘life-events’ in the introductory explanation. It was explained to them that their house, rather than their name, had been selected at random, and quite often the interview was completed without the interviewer discovering the woman’s name. although most were quite happy to give it. The interviewers were highly motivated to minimise the refusal rate, and would spend many minutes on the doorstep persuading people that just because they had no health problems it did not mean that there was no point in interviewing them. One woman was visited some 15 times before she finally agreed to participate (the other fourteen times she kept giving plausible reasons why she could not be interviewed on that particular day). The percentage of refusals was 170/h which, given the nature and length of the interview, compares favourably with other surveys. Our worry was that women in the community who had recently experienced severe events might be less willing to be interviewed, thus artificially lowering the rate of events in the comparison group. But to assume that such women are ‘normal’ rather than cases of depression is quite a conservative assumption, and perhaps more likely is that those refusing are more depressed than those agreeing. Subsequent consultation of the Camberwell case-register gave some hint of this for the second series of women seen in Camberwell. (Unfortunately it was not possible to do this check for the first series). However, with a refusal rate of only 17x, such biases, even if they did affect our data. would hardly overturn the direction of our results. (3) CASES
IN
THE
COMMUNITY: WITH
DEPRESSED
HOW
COMPARABLE
ARE
THEY
PATIENTS’?
Shapiro seems to have been confused by our five-point severity scale at this point. He argues that because only I 1% of our cases are on the top two points of this scale they are therefore likely to be ‘normal’ women undergoing ‘signs of stress’. He fails to see that the same conclusion must logically apply to the 56% of the depressed out-patients who were rated on the bottom three points of the severity scale. The crucial threshold is clearly not between the top two and the bottom three of these five points but between the fifth point and the category of reactions which we labelled ‘borderline cases’ and included in the ‘normal’ group of women for purposes of our analysis. This threshold, between ‘case’ and ‘borderline case’, when examined later after the publication of the Feighner criteria for depression, was surprisingly similar to that of Feighner and his colleagues (cf. Brown and Harris, 197Sa. pp. X3-59; Feighner et al., 1972). Shapiro is worried that by excluding these ‘stress reactions’ from our comparison group we have artificially lowered the rate of severe events in this group. It might reassure him to know that in assessing the importance of life-events in bringing about depression we used a measure of association which takes account of the chance juxtaposition of event and disorder and that the wlzole general population including both ‘cases’ and ‘normals’ was used to calculate the base rate of severe events in the formula (op. cit. Chapter 7, pp. 117-121). (As will be seen there are other reasons why it is unfortunate that Shapiro did not read Chapters 7-14 of our book.)
603
GEORGE W
BROW
and TIRRIL HARRIS
Shapiro refers to Tennant and Bebbington’s paper reviewing our book in connection with this issue of caseness but not to our reply (Brown and Harris. 1978b; Tennant and Bebbington. 1978). Perhaps he decided not to bother to read that too. We do not have space here to repeat the many points made in that reply. but it should be stressed that our measure of caseness is much stricter than those used in most recent population studies of psychiatric disorder (see also Finlay-Jones and Murphy. 1979). The real problem which bedevils this issue is that no-one has yet developed criteria other than the two we use (severity and duration) which can be used objectively (sic) to distinguish stress reactions from clinical depression. We should however state at the outset that many authors who discuss transient stress reactions are dealing with wry transient ones, lasting a week or less. For example Duncan-Jones and Henderson (1978) described how in research using a two-stage design, first screening with the GHQ and then giving a PSE later, there were often discrepancies between the responses on the two by the same person, especially if more than a week elapsed between the stages. Our cases were required to have experienced a minimum duration of symptoms of lOdays. regardless of the intensity. In practice the shortest ‘episode’ we recorded among the cases was four weeks. The interviewers supplemented the shortened version of the PSE with a number of questions about the course and fluctuation of symptoms, but since the majority of cases had not recovered during the year before interview this information only gives us assurance about the minimum duration of episodes, not about their overall duration. Only detailed follow-up studies tracing the course of episodes until the point of recovery, and comparing community cases with psychiatric outpatients, will clarify whether there is any more than faith to support the notion of the difference between a distress reaction of a certain severity and of minimum duration and a ‘real’ depression. We suspect if a criterion ever does emerge it will relate to some feature of personality organisation, the measurement of which will be very complicated. In the meantime progress can only come from sorting subjects as we have done into groups of comparable symptom severities. One final point on this topic: Shapiro says that it would be worthwhile comparing event scores of each of the various sub-groups. At different points in the book we do in fact do this (e.g. Chapter 12 looks at ‘borderline cases’ separately from the other women and Chapter 13 compares in-patients and out-patients). (1)
THE
MEASUREMENT
OF
LIFE-EVENTS
(a) Validitj Shapiro is unwilling to accept our patient-relative agreement study as a form of validation. While it is, of course, true that family folk-lore may exist about events this does not imply that such a study is meaningless in terms of validity. It is in any case inconceivable that a complete check on validity could be done without interviewing others who knew the person. Only a minority of events have some kind of public record and in using records of say deaths, marriages, births and hospital admissions as checks on validity it is infinitely easier to locate ‘false positives’ (e.g. a death reported by the subject but not recorded officially) than it is ‘false negatives’ (e.g. to find about ‘missing’ deaths one would not only have to run through all registered deaths in the country but also check their attachments to the person concerned). Since our research grants did not run to the latter monumental undertaking we confined our formal test of validity to a patient-relative agreement study (which allows the checking of both false negatives and false positives). In this comparison we found for severe events (i.e. those of causal importance) a 91% agreement between patient and relative about the occurrence of specific events. We believe we had every justification to be impressed by this result and that it represents an important test of the instrument’s validity. The level of agreement may however appear less surprising when it is’ remembered that severe events represent incidents of considerable importance such as a husband leaving home, death of a parent. birth of a baby and life-threatening illness of someone close. The importance of these events also explains why we were not concerned with bias from ‘family folk-lore’. We find
The sin of subjectlvism:
A repI> to Shapiro
605,
it difficult to believe that the events had not in fact occurred. What influence therefore could reasonably be expected from such folk-lore? The only possibility that occurs to us is that in some way the date of the event could be confused. Here we made an effort in the earlier study of schizophrenia (Brown and Birley, 1968) as well as in the work on depression to check the dates of important events with ‘public records’. This extremely rarely led to a change in the time ordering of the event and onset. If any systematic bias for events to be dated before rather than after onset has crept into our results, there are however implications which Shapiro does not follow through in his critique; for there would then be a much higher rate of severe events after onset among the depressed than among the normal women which would require elucidation. The only reasonable explanation for this would then be that the depressive disorders had somehow brought about the severe events. Since we had used a measure of the ‘independence’ of events (their independence that is of the behaviour of the respondent) we could examine this alternative notion: how feasible is it to say that the high rate of severe events could really be due to the respondent’s activities under the influence of depression, and that biased reporting had placed them incorrectly before rather than after onset? On pp. 103 and 347 we give figures which show that depressed women experiencing severe events which were on logical grounds likely to be largely ‘independent’ of their volition were more than four times more common than those experiencing only severe events which may somehow have been brought about by their own actions. When considered separately both types of severe event showed the same order of association with onset of depression. It makes no sense to suggest that, say, a letter from the Council notifying one of the imminent demolition of what has been one’s home since childhood (an obviously ‘independent’ event) could happen more frequently in a group of women just because they were already depressed. Shapiro ignores our measure of ‘independence’, but we feel that our results on this dimension clearly support the conclusion that no really important bias has crept in to our dating of events and onsets. (b) Dimerisiorrs of‘/ife-ecetits Shapiro complains that the scales describing events are not presented in full. He must have missed pp. 95-97 of our book where they are given in full to describe two events in detail. He says we do not give details of the reliability of the threat rating but in fact we do in a footnote to Chapter 5, p. 346. Shapiro says we do not make explicit the criteria for the ratings. In fact the whole chapter on ‘Meaning’ does so in general terms; of course to do so more specifically in the sense of enabling someone to repeat our ratings, would have involved a lengthy discussion devoted to each different type of event probably taking well over one hundred pages of text. This was clearly inappropriate in our book. However, we do have both a Dictionary of Threat Ratings and a Training Handbook if anyone needs the detailed criteria, and we provide these to interviewers who wish to train in our methods. (We have now successfully trained more than a score of other workers in these ratings.) We should perhaps also mention a paper by Tennant et al. (1979) which reports a reliability study of ratings of severity of the contextural threat of events made during our team rating meetings. This concludes that the ratings can be made with very satisfactory reliability. Having dealt with the chronicle of our ‘mistakes’ it will be clear that we have been just as concerned with the possibility of bias as Shapiro himself. His suggestion that as ‘relative subjectivists’ we do not look critically at the way we collect and analyse data is false. It is precisely because we have been so concerned that we have measured things in the way we have; for we see a great distinction between the demand to minimise bias, which we accept as essential in scientific research, and the need to minimise subjective judgements by investigators. The first does not require the second. So long as judgements by investigators can be made reliably there is nothing necessarily wrong with using definitional criteria to which the subjects of the study are not party. Since there is no dispute about the need for reliability we will start with Shapiro’s use of the term ‘subjectivity’. One meaning is linked to the idea of reliability: when criteria
610
GE~RCE W. BROW* and TIRRIL HARRIS
are private there can be no guarantee of reliability. that is comparable and repeatable use of descriptive categories. One just has to trust that when the person talks of. say anxiet) states, on one day he is using the same criteria as he used on another. In this sense our study was not subjective. Our criteria for ratin g were almost tediously public. We spent much time developing criteria defining the boundaries of our categories such as events and their dimensions which were then embodied in a manual and no interviews were included in the survey until the interviewer had undergone a lengthy training in their use. Critical ratings such as those concerning the threat of events or psychiatric ‘caseness’ were always brought to weekly rating meetings and re-rated by the whole research team (without prior knowledge of the interviewer’s rating.) This procedure even on the most complex ratings produced high reliability standards which bvere public and shared.* Another meaning of subjective is that, despite being public and shared. the standards are still not shared by everyone: they are only shared by a group of individuals. In this sense our work is ‘subjective’; and for this we make no apology. It had to be by the very nature of the project we were investigating. Different people define in different Lvays what is and what is not stressful: what is and what is not depression. There never will be a miwrsaIly acceptable set of public criteria. Under such circumstances there are three possibilities open to an investigator: one is to take the subjectivity of his respondent as his defining principle-anything defined by the respondent as stressful he will accept as stressful, anything defined by the respondent as depression he will accept as depression. A second course is for the investigator to apply standards of his own, and to make these public and repeatable. And a third is to give up all hope of investigating the area because of the lack of objectivity. Shapiro berates us for choosing the second course. but there are so many pitfalls attendant on the first that if he cannot find it in him to accept the second course the only option he has left is the third, to give up any attempt to study this topic in causal terms. But just before we outline the pitfalls of the first approach, it is worth saying that when we chose the second approach as the main basis of our analysis we did not shun the first completely. The team assessment of the conte.stual threat of events was based rlor on our estimate of how \t’e would react to an event of particular kind, but on how we thought the majority of people in similar biographical circumstances would react to it. We were not therefore using our own reaction to the event but our judgement of how most women would feel about it in the circumstances. While the latter procedure is, of course, subjective, it is not so in quite the same way as the former would be. It should also be noted that in making such contextual ratings the team of raters were not told how the woman said she had responded to the event. It was essential to do this in order to rule out important possible sources of bias. If we had allowed such self-reports to influence the contextual threat ratings we could never have hoped to rule out the dangers attendant on the first of the three strategies. We have devoted much attention in one of the chapters read by Shapiro to the pitfalls of choosing the respondents’ rather than the investigators’ definitions. We maintain that this can introduce not merely random errors, but a systematic bias either of ‘direct contamination’, ‘indirect contamination’ or ‘spuriousness’ (op. cit. pp. 73-81). As a quick example of one of these, consider the possibility that the more anxious, despite having exactly similar experiences to their less anxious counterparts. may see life-events such as illnesses of a close relative as more stressful and report them more often in answer to general questions about illnesses in the family. But, if it is their anxiety and not the events they report that gives rise to their depressive disorder. the association between events and depression would be spurious. not causal. We can be confident that our data is not contaminated in this way because we guarded against this bias both at the stage of interviewing and of rating. At interview we did not ask what had been found upsetting but only about the occurrence of certain events irrespective of the respondent’s reactions to them; we were careful to probe in a way that facilitated the remembering of events by * L+‘rbelievr that the term O~/YCII~.CIS best used to describe reliable measures. ment between Independent ratrrs IS a particularly important form of rrllability: ‘intersubjectivity’ (Galtung. 1967, pp. JS-29).
For soaologlsts what Galtung
the agreehas called
The sin of subjectlwsm:
A reply to Shapiro
61 I
people whose less anxious personalities might have gone with a tendency to give less prominence to anxiety-arousing experiences, with a consequent tendency to recall them less readily than their more anxious neighbours. When it came to the stage of rating the tape-recorded information the many rules for inclusion or exclusion of events ensured that the same standards were applied to both the anxious and the less anxious respondent: thus many of the illnesses mentioned by the more anxious subject would not meet the criteria for inclusion on the rating schedule. Furthermore. as we have already emphasised. once the details of an event had been collected we ignored the woman’s reported reactions to it in rating contextual threat. Shapiro is quite right to point out that the PSE is like the life-events interview in exactly these ways. This is why we chose it. A semi-structured interview with probes, it takes the interviewing team’s definition, for example. of ‘delayed sleep’ as the criterion for a positive rating, not the respondent’s definition. For with symptoms as with life-events there may be systematic reporting biases. For example, a more highly defended person may say they have not really been all that depressed and another person say that they have ‘really been feeling dreadful’, but it is only on probing that it emerges that the second person can always be cheered up when someone else comes in whereas the first has often sat in company trying to participate and feeling low throughout. (The more defended person may also be less anxious and so recall life-events less readily without extra reminders.) There is a long and respectable tradition in psychology which tries to correct for ‘response-sets’ and which acknowledges such reporting biases. But there is also a tradition which encourages the use of paper and pencil questionnaires, a feeling that they are somehow safe, sterilised from the interviewer biases which are an inevitable part of face-to-face interviews. The sins of interviewer bias are considered at the expense of noticing respondent bias. Although Shapiro does not devote much space to it we suspect that what underlies all his other criticisms is his worry that our work may be subject to interviewer-bias through halo-effects. Of course it is quite true that the same interviewer collected both life-event and symptom data in the general population and out-patient samples, and that such a procedure could lead to differences both at the stage of data collection and of rating in the way ‘cases’ and ‘normals’ were treated. For example. a woman with obvious depressive symptoms might be more closely questioned for events, or there might be a tendency to rate her events as more severe than those of a normal woman. One way of controlling for the latter (at the stage of rating) is our procedure of team rating meetings where the events are presented to raters who are blind to knowledge of the woman’s symptoms, and vice versa. A way of controlling for the former (at the stage of questioning the woman) is to ensure that the interviewers are trained properly in unbiased interviewing. This involves establishing an ethos in which interviewers are taught almost to be biased in the opposite direction from the hypothesis which they cannot fail to know they are helping to test. Our interviewers were taught to keep on probing for life-events with ‘normal’ respondents if anything longer than with ‘cases’. Conservatism (in terms of the hypotheses to be tested) was also the guiding principle at the stage of rating if ever there were uncertainties in deciding for example between marked and moderate long-term contextual threat; (for we are not pretending that such uncertainties never arose-life is fortunately more varied and idiosyncratic than the specifications of our training manual, and new standards had to be created from time to time.) Under such circumstances events occurring to patients were nearly always rated down (as less threatening) on principle (for greater detail about this cf. op. cit. pp. 147-149). Finally in assessing the likely degree of bias in our work there is a further form of validity to which psychologists have given a good deal of attention and which Shapiro entirely ignores; this is ‘construct validity’. It is an interesting form of validity because it depends on the relationship of actual results of the research to predictions made either on logical or theoretical grounds about them. There is an element of ‘the proof of the pudding is in the eating’ about this approach and as with puddings it can take many
hi’
GEORGE W. BROW\ md TIRRIL H,ARRIS
forms. Thus in our own work we place considerable importance on the fact that although severe events form only 169, of all the events occurring to women in Camberwell. it was only these severe events that played a formative causal role. a result repeated in three separate studies (op. cit. Chapter 7). The logical point is that if there had been significant bias stemming either from the interviewer or respondent one would not have expected the association to occur only for one fairly infrequent type of event but to have applied also to other events. Furthermore. events severely threatening only in the short-term (a child nearly dying but recovering within a week) showed no association whatsoever with onset of depression. We are convinced that these results were in no way anticipated by the raters and it is hardly convincing to argue that our respondents themselves made such distinctions. Probably as great a danger facin g any academic discipline as that of bias and error in its measures is the turning of a once effective technique into ritual. The sense of safety which the use of a well established pencil and paper fired-choice questionnaire can bring is an example of just such a ritual. The streamlined procedure lends speed to the analysis of the data and discourages potential critics like the label from a prank--cru vineyard. But this does not mean that other wines cannot have their own particular value. Face-toface interviewing allows so many things which can enhance validity if interviewer biases are properly controlled-for example difficult words can be defined for the respondent’s benefit. All too often a respondent will say “well that depends”. and it can be of great importance on what it depends, in which situations that personality item is true of him and in which it is not. Paper and pencil questionnaires cannot usually provide enough alternatives to account for all these situations straightforwardly, while verbal interviews can usually resolve the matter. The interest in situationally specific measures of personality over recent years suggests that psychologists are now beginning to reaiise how much valuable information can be missed by generalised questions (Mischel, 1968). It is a pity that these moves tend to be seen in terms of new theoretical perspectives rather than as a means of circumventing totally inadequate methods of measurement. The use of tones of voice can be of crucial importance in measuring certain features of the home environment which are significantly related to relapse in schizophrenia [cf. Brown, Birley and Wing (1972) and Vaughn and Leff (I 976); for detailed discussion of the development of these measures cf. Brown and Rutter (1966) and Rutter and Brown, (1966)]. The creative way to confront these areas is to develop methods of measurement which capitalise on the advantages of face-to-face interviewing while imposing maximum control on interviewer bias, not to retreat into the time-honoured instruments which can miss the crucial dimensions concerned. There is an obvious danger in replying to such provocative criticism that one may seem arrogant in one’s own defense. Having emphasized the advantages of our ‘subjectivist’ approach and stressed the efforts we took to minimise bias, we have no wish to convey the impression that no improvements could be made in our work. The study was naturally subject to the restrictions imposed by time and money. and doubly so because it was largely pioneering; life-event research had not been done in this way before in Britain. Now that its feasibility is accepted we have been fortunate enough to obtain further funds for a prospective study in which some of these improvements can be made. The obvious advantage of a longitudinal study over a cross-sectional one is the greater certainty in ruling out the reporting biases which experience of a depressive episode may introduce into the recall of retrospective data. (As we have already conveyed we do not believe that important bias is likely for the life-event material but it certainly is a possibility for some of our ‘softer’ measures such as intimacy.) It will be possible in this much larger study to introduce checks and refinements not possible in a study without follow-up interviews-for example, if a respondent has initially agreed to participate with several interviews it will be possible for two different interviewers to be used, one asking only about life-events without any questions about symptoms. A small sub-study comparing the results of this interview with those of the main interviews would provide further surety on halo-effects and interviewer bias. Follow-up too should allow a much
6 1;
The sin of SubJectivlsm: .A rep{? to Shapuo
more subtle approach to the caseness-borderlineness threshold. As in earlier research with schizophrenia it is necessary to move in this way from cross-sectional to prospective designs (see Brown, Birley and Wing. 1972). In the end scientific advance usually comes from the convergence of many different lines of evidence; from several methods of approach rather than from a ‘definite experiment’ which is beyond reproach. Sin in measurement is not in Shapiro’s subjectivity but in the belief that it is necessary to find methods that are beyond all reproach-it is a sin because it leads either to hopelessness about what can be done or to blind faith in a limited technique. We are convinced that a truly effective and creative social science must be built round the kind of empathic measurement discussed by Max Weber and others in terms of rersrel~en and which we have attempted to develop. Our confidence in our results stems from the flexibility of this approach and its ability to use the most sensitive of all measuring instruments-the human mind. Shapiro’s view therefore both of our errors and of our philosophy of measurement is inaccurate; we hope that this reply will be enough to convince readers to look further at our book and judge for themselves the merits of our methods. ~cl;,lo~~l~dgrnrrrIt-Ws Register.
are grateful
to Jane Hurry
for her help in the use of the
Camberwell
Psychiatric
REFERENCES Brows G. W. and RUTTERM. (1966) The measurement of pamily activities and relationships: A methodological study. Huv~nn Rel. 19. 241-763. BKO~VU G. W.. BIRLI:\I’ J L. T. and WING J. K. (1972) Influence of family life on the course of schizophrenic disorders: a replication. Br. J. P.s.rcltiaf. 121. 1-i-25s. BROWN G. W. and HARHIS T. (I978a) Social Orlgirrs o/ Drprrssiopt. Tavistock, London. BROWS G. W and HARRIST. (1978b) Social Origins of Drprrss~on: a reply. Psycho/. Mrd. 8. j77-5YY. BROWS G. W. and BIKLEYJ. L. T. (1968) Crises and hfe changes and the onset of schizophrenia. J. Healrl! sot. Brh. 9, 203-214. DL~CAS-JOS’ES P. and HESDEKSONS. (1978) The use of a two-phase design in a prevalence survey. Sot. PS)C/IiUf. 13, 23 l-737. FINLAY-JONFS R. A. and ML’KPHY E. (1979) Severity of psychiatric disorder and the 30-item General Health Questlonnalre. Br. J. Pvycl~ic~r. 134. 609-616. GALTUSG J. (1967) Theory nrld Mrrhods o/~Sociul Research. Allen and Unwon. London. MISCHEL W. (1968) Prrsorul~ry and Assessment. John Wiley, New York. RC’TTVR M. and BKOWN G. W. (1966) The reliability and validity of measures of family life and relationships in famllies containing a psychiatric patient. Sot. Psychor. 1. X-53. TES\A\IT C. and BEBHI~GTOX P. (1975) The social causation of depression: a critique of the work of Brown and his colleagues. Ps~cl~ol. hlrd. 8, 565-575, TI SUST C.. SMITH A.. BEHNSGTON P. and HURKI, J. (1979) The contextual threat of life-events: the concept and its rcliabillty. Ps~.ho/. .\fvc/. (in press). VAUGHS C. and LEFF J. (1976) The intluence of family and social factors on the course of psychiatric illness: a comparison of schizophrenic and depressed neurotic patients. Br. J. Psychiur. 129, 125-137.
