Positivism, hermeneutics, and phenomenology

Tullio Carere-Comes, editor

Editor's note. I have edited here my own contributions to the JAPA Online Faculty Seminar in which Luyten, Blatt and Corvelyn's 2006 paper " Minding the Gap Between Positivism and Hermeneutics in Psychoanalytic Research", Japa 4, 2, was discussed. The discussion lasted from September 15 to October 16, 2007. All contributions can be read in the JPN Archive, where one can also find a rich summary of the discussion by its moderator, Robert White. My decision to collect here my own contributions is justified by the fact that in each intervention I quote or summarize other authors' interventions to which I am responding. Therefore, the series of my contributions can be read as an essay in which I expose my ideas on positivism, hermeneutics, and phenomenology in a cross-talk with the other contributors.

Tullio Carere, September 15, 2007

The key to my understanding of Luyten, Blatt and Corvelyn's paper is in the following sentence: "If we really want to convince our patients and the public (as well as ourselves) of the value of psychoanalysis, this necessarily entails theories that propose probabilistic regularities in human behavior" (p. 581). The great divide that LB&C point out could be described in the first place, in my view, as the one between those who don't need to be convinced of the value of psychoanalysis (the true believers), and those who do need to be convinced (the lukewarm believers). If this is the divide, I would say that it is not so great after all, because it is not really so difficult to warm up the lukewarm and restore their faith. As Rosenthal (1991) has  shown, researchers usually find what they expect to find, and empirically oriented researchers are no exception to this general rule (LB&C remind us that about 70 percent of the variability in effect sizes reported in outcome studies could be attributed to researcher allegiance to a particular therapy). LB&C aptly quote Luborsky et al's 1999 paper, to which I would add Luborsky et al's 2002 paper ("The Dodo bird is alive and well--mostly") in which they examine 17 meta-analyses of comparisons of active treatments with each other and find a small and non significant effect size, which becomes even smaller and even less significant when such differences are corrected for the therapeutic allegiance of the researchers involved.

Psychoanalysts have lagged behind in the Dodo bird run, and now they try hard to catch up with the group in order to gain the scientific respectability that other schools have already gained--and, of course, they also hope like everybody else to kill the bird in the end and win the race. But, in the meantime, the bird's verdict (all have won, all deserve a prize) holds. What should one do at this point? I, for one, endorse LB&C's plea for the search of regularities in the field, but I would leave out the adjective "probabilistic", which seems to imply the necessity of quantitative-statistical research. The current emphasis on quantitative research is based on the assumption that the methods of natural sciences could counteract the tendency to tailor data to fit theoretical notions that is the weak point of the case study method. But this assumption is wrong. Empirical researchers are as biased as their clinical counterpart, and their empirical methods are as ineffective as the traditional ones to neutralize their biases. The researcher allegiance operates equally well in the two approaches, with the result that both kinds of researchers wind up finding what they expect to find. The Dodo bird is very happy in this state of affairs, because this means more and more food for it. Yet I don't think that bridging the gap between two wrong assumptions is a good idea.

Is there a better idea? Yes, I think there is one, but it is unlikely to be appreciated by those who want to convince themselves and others of the value of their thing--psychoanalysis, or whatever. The idea is that the very idea of convincing anybody of anything should be abandoned, if science is to begin. This means to take an attitude of suspension of all preconceptions and expectations in the study of phenomena, the one that is called epoché in phenomenology (maybe "freedom from memory and desire" sounds more familiar to psychoanalytic ears). With this attitude (the establishment of which requires, as both Husserl and Bion warn, a permanent, durable and continuous discipline) we study what transpires between a patient and a therapist who meet regularly in a room, NOT what is generated by a theory whatever. As Friedman (1997) pointed out, "Freud did not design a treatment: he discovered one". If it were not so, Friedman points out, therapy would be an arbitrary venture: "If I am wrong in my assumption--if treatment is just the application to patients of whatever analytic theory happens to be knocking around at the moment--then my method is pointless". In this bottom-up approach we let the process develop according to its own logic, and then study this logic. In the top-down approach, instead, one ties the process to the Procrustean couch of one's theory, and studies the resulting artifact.

What we observe, if we really want to observe, may or may not be in accord with our cherished theories, psychoanalytic or else. Yet if we want to stand on a scientific ground, we must be prepared to accept that the regularities we observe may or may not be called psychoanalytic, whatever is the meaning we give to this word. Being a scientist and not being willing to put one's allegiance at stake is like wanting to have one's cake and eat it.

Tullio Carere, September 16, 2007

Howard, why should we have a psychoanalytic model of health? Why couldn't we leave to the individual patient, or the individual analytic couple, to decide the goal of the treatment?  To be free of one disturbing symptom or problem is a bliss to one patient, and she does not want anything else for the time being. To another self-knowledge and personal growth is what really counts. But I see your point: you are "concerned that research (qualitative, N=1, quantitative, ...) would be helter-skelter", unless it is guided by a general agreement on the goals for a successful analysis--though you admit that this agreement does not and most probably will never exist. My concern is the opposite. Research is necessarily helter-skelter to the extent that it is guided, as in fact it is in our field, by what researchers consider to be the goals of the treatment, i.e. their theories. They want to have their theories validated or corroborated, and they get what they want. Sid believes that the vulnerability to allegiance effects of both the probabilistic-scientific and the hermeneutic-interpretative approaches could be neutralized by multiple approaches, by different investigators and clinicians with different theoretical commitments. I believe that this belief is justified in the hard sciences, where different theories come up against hard facts, much less or not at all in a field like ours, where meanings are overwhelmingly more important than facts (an interpretation is not a hard fact, it is not even a fact, its effect depending on the patient's interpretation of the analyst's interpretation). This is why I say that there is no way out of the proliferation of theories and the pulverization of the field, other than through an approach that brackets out all theories.

Tullio Carere, September 17, 2007

Do I want to convince others, as Paolo Migone maintains, that a theory-free approach is better, and more scientific, than an empirically supported one? Maybe the opposite is equally true: I want others to convince me that an empirical approach is more appropriate for our discipline. In a forum like this the rule of the game is, as I see it, that everybody brings forth his or her ideas and try to support them with the best possible arguments and evidence, but open to the arguments and the evidence of the others, to the end of a frank and fair confrontation. I do not believe that there is only one science, as some (especially in the empirical science field) believe. To me, there are many. The question is: which scientific approach is more suitable for psychoanalysis and psychotherapy?

Many supporters of empirical science use to dismiss the phenomenological approach as mere "good will", as "immaculate perception", and so on. Let me try to explain. To be theory-free does not mean that one has no theory (I personally think that it is good to have many theories in one's quiver): it literally means that one is free to use any theory one deems appropriate to the present case (or none at all), without belonging to it. Theory freedom means no allegiance to any theory. Theoretical allegiance brings to devotion, belief, as in the case of Marie Bonaparte quoted by Uebel. Theoretical freedom is, in my view, the correct scientific attitude in general, and in our field in particular. Of course, this freedom can never be complete. One has to work hard to be freer and freer. We can easily appreciate the difference, for instance, between a journalist who tries to be objective, constantly taking a critical distance towards his own opinions, and another bigoted and factious, who never practices this discipline (the sentence also works with "psychoanalyst" in the place of "journalist"). The discipline must be deliberate, and "permanent, durable and continuous", as Bion pleaded. It should not be taken for granted, nor should it be dismissed, as many do when they say that all observation is theory laden--implying that there is nothing to do to make the observation as theory-free as possible, and the only thing to do is put the theory to empirical test. In this way empirical science can easily be used as a defense against the effort of personal discipline.

I will try to respond from this point of view to Bob White's question:

"If there are multiple defenses, how do we assess which defense is

operational at any one point in the hour and thus can be interpreted?

Is there any way to assess which interpretation may be more effective at

any one point?  Can we study blending of technique, where the analyst

uses a blend of both techniques when she feels it is appropriate?  How

can we assess if they are effective in further the aims of analysis?"

In my view in order to assess which defense is operational at any one point it is good  to know the pattern of as many defenses as possible, but first of all one has to keep in mind that anything can be a defense against anything else (I have just pointed out that empirical science can be a defense against theoretical freedom, and of course phenomenology too can be, and in fact is, a defense against therapeutic interaction, when it clings, as most phenomenologists do, to a passive, contemplative attitude--which has brought about outstanding contributions to psychopathology, but almost nothing to psychotherapy). What is a defence to what and why, can be best decided on a contextual basis. Then, to assess which interpretation may be more effective at any one point, we rely on our experience  and that of our colleagues, and our clinical intuition, but it is mandatory to assess the effect of our interpretations with the help of the patient's feed-back, and of the events that follow our intervention during and after the hour. In this sense the analyst is a "local scientist" (Stricker & Trierweiler, 1995), inasmuch as he/she transforms all of their intuitions in hypotheses to put to test in the therapeutic relationship. Blends of techniques are used by most analysts, but the study of these blends and the assessment of their effectiveness can only be done, in my view, from a theory-free standpoint, because any theoretical allegiance introduces a bias which either is contrary to any blending, or claims the primacy of one theory over all the others in the blend. I see theoretical freedom as the best antidote to bigotry, which is not a rare occurrence in psychoanalysis and psychotherapy.

Tullio Carere, September 20, 2007

Jerome D. Frank (thanks to Henry Friedman for reminding us of his groundbreaking work) devoted his whole professional life to psychotherapy research. In the epilogue--his scientific legacy--of the third and final edition of "Persuasion and Healing" (1991) he wrote: "Over the years I became increasingly puzzled by the contrast between the methodological sophistication of the research conducted by many outstanding psychotherapy researchers and the triviality of most of their findings...Suddenly the light dawned. As a type of persuasion, psychotherapy might be more closely allied to rhetoric and its close relative, hermeneutics, than to behavioral science!...Could the fundamental limitation of psychotherapy research be that researchers have been trying to apply to the realm of meanings methods created to elucidate facts?"

First point. It is not that empirical research in psychotherapy does not yields results. As Paolo Migone rightly points out, once discounted the 70 per cent of the researcher allegiance, there remains a good 30 per cent of valid results (by the way, I would roughly assign a similar percentage to the case study method, the two approaches being more or less equally biased--but the two biased approaches in my view compound their respective biases, rather than mitigate them). Empirical research does yield results, but these results are mostly trivial--i.e., they "while statistically significant, have been too weak to influence clinical practice. Moreover, many unnecessarily elaborate experimental designs have merely examined minor variations in methods or concepts or confirmed common-sense conclusions" (Frank). The triviality of these results explains why, as everybody knows (and H. Friedman reminds us), empirical research hardly has an impact on clinical practice. Clinicians simply don't read the empirical research papers, which they find boring and irrelevant to their work. Are most clinicians lazy, ignorant, and arrogant or is there something very wrong in most empirical research?

Second point. As some may suspect, I am inclined towards the latter option. My response to the question: "what is wrong in most empirical research?" is the same as Frank's: it tries to apply to the realm of meanings methods created to elucidate facts. Westen et al (2004) trace the many fallacies of empirical research to its behavioral science approach and question the "highly problematic" Popper's principle that the essence of science is hypothesis testing (the context of justification), whereas the formulation of hypotheses (the context of discovery) is left to mere undisciplined intuition or subjective whim. In a similar vein, LB&C write: "if much of the 'good stuff' in psychoanalysis comes from the case study method, why should we consider it as suited 'only' for the purpose of generating hypotheses? Rather, shouldn't we try to improve this method, so that it becomes more scientific?". In fact, the context of discovery could and should become a scientific enterprise in its own right, free from the suffocating tutorship of the context of justification--though sure enough, my idea of what would make the context of discovery scientific differs substantially from both Westen's and LB&C's. However, in spite of this noteworthy support to the autonomy of  the context of discovery, much of  LB&C paper seems to be still rooted in a behavioral science approach to research, which studies correlations between therapist's behaviors ( e.g., an interpretive behavior) and therapy outcome.

Third point. The light that dawned to Frank seems to dawn to more and more researchers today, who abandon the behavioral approach. For instance, researchers of the Control mastery theory (Silberschatz, ed, 2005) study the disconfirmation of pathogenic beliefs as a common factor across therapeutic practices, independently of the theory and technique of the therapist. This is a big step forward, although only halfway in the right (to me) direction, to the extent that they suspend all theories (of the therapists) but one (theirs). What I still see as a fallacy in this trend of research, in spite of its great progress in comparison  to the behavioral approach, is the new myth that  pervades it: the new magic formula of inter-rater reliability. Nothing to object to inter-subjectivity as a form of objectivity, to the contrary. My objection regards only the fact that inter-rater reliability is still based on the theory of the researcher. Because of the researcher allegiance effect, it is all too easy to anticipate that researchers will go on validating their cherished theories. Paolo would object that they would be anyway 30 per cent objective. Granted, the same as before. We are heading for a new lap of the Dodo bird run.

I would like to make clear that I am not against empirical research, not even the more behavioral form of it. I simply don't regard it as useful, because my logic finds it faulty and my practice has never been enriched by it in any meaningful way. But if others like it and find it useful, fine, nothing to object on my part. What I do strongly object to, is the claim that empirical science is the *only* true science, and we should all submit to its rules. This is not science, it is scientism--that is an ideology according to which there is only one science and those who don't believe in it are infidels. For instance, Patrick Luyten says: "As philosophers of science have pointed out, all observations are 'theory-driven', and without theory, we would see nothing." All observations are theory-driven, and those who don't believe in this dogma are infidels. Husserl wrote "The crisis of European sciences" to show precisely that the identification of science with empirical, quantitative science is the main cause of the crisis of Western science (and Western society), and all his work is devoted to the task to make clear that we return "to the things themselves" only to the extent that we learn to look at the world without the filters of our theories, judgments and expectations. Are Husserl and all the phenomenologists not "philosophers of science"? But I personally don't need to stand on giants' shoulders to say what I say. It is enough for me to  realize that to the extent that people stick to their theories (or hypotheses, or beliefs) they see only what their theories or beliefs allow them to see. We can see something new and something real only to the extent that we are willing to suspend our preconceptions, which can only give us a preliminary understanding of things. In Piagetian terms, if it were true that all observations are theory driven, we would go on assimilating all experience to our previous schemata. Only to the extent that we are willing and capable to suspend them, we begin to see something new, which allows us to accommodate old schemata or create new ones--and we can also, and above all, remain in that suspension (Keats' negative capability: "when a man is capable of being in uncertainties, mysteries, doubts, without any irritable reaching after fact and reason"). And, above all, only in the space open by the suspension of all preconceptions and expectations--memory and desire--true dialogue happens. This is what my logic and my experience tell me. If others think and feel differently, fine, I can disagree but I unconditionally respect their different experience. I am very happy when others do the same with me.

Tullio Carere, September 22, 2007

Just a note on Westen. On more substantial issues (my "extreme relativism"), later.

Patrick Luyten wrote: "I think this [mine] is a serious distortion of Westen et al.'s paper, in that Westen et al. showed that some of the assumptions underlying current psychotherapy research are wrong, not the methods that were used." If we are discussing of the same paper (Westen D., Morrison K. & Thompson-Brenner H., The empirical status of empirically supported psychotherapies: assumptions,    findings, and reporting in controlled clinical trials. Psychological Bulletin, 2004, 130:631-663), I think that Patrick is wrong. In this paper Westen et al clearly state that not only many of the assumptions of the ESP are wrong, but the method is basically faulty inasmuch as it is not theory-neutral, being based on fundamental assumptions of cognitive-behavioral therapy, or at least the cognitive-behavioral therapy of the late 1970s.

Tullio Carere, September 22, 2007

I wrote that most empirical research is to me, as to most clinicians, trivial, i.e. irrelevant to practice. Most, not all. There are some significant exceptions, one of which is the Menninger Psychotherapy Research Project, whose results are best summarized in Wallerstein's classic "Forty-two Lives in Treatment" (1986). Its most noteworthy result is not trivial, because it falsifies the basic assumption of the Project and the most cherished psychoanalytic myth: no significant difference was found in the outcome between psychoanalysis and expressive-supportive psychotherapy. This result was important for me, not because it debunked a myth (which I had already debunked for myself at that time: in this respect the result for me was trivial), but because it highlighted two basic levels operating in all therapies, however labeled: the expressive-interpretive and the supportive-stabilizing. I did not agree completely on the way these two levels were connoted and called, but the distinction was anyway fundamental to understand how all therapies work.

I was disappointed when, years later, the conclusions of the MPRP were challenged by Blatt and Shahar (2004). I read the paper, that Sid kindly sent to me, and found nothing to object: a difference between psychoanalysis and psychotherapy did exist, if the difference between anaclitic and introjective patients was introduced. But now, as I was preparing to explain how I am not an "extreme relativist", I re-read Blatt and Shahar's paper, and this time I did find something relevant to object. They write (p. 395-396):

Wallerstein (1986) described PSA in the MPRP as operating “essentially through the establishment of a full-fledged regressive transference neurosis, and its ultimate resolution comes about centrally through interpretation leading to insight and mastery” (p. 54; see also Gill 1984, 1988). According to Wallerstein, SEP in the MPRP is “similar to psychoanalysis in mechanism but differs sharply in degree.  It is limited in focus to agreed-upon sectors of psychic distress and per-sonality malfunction. . . operating through means that do not evoke a full transference regression, all leading to less extensive (more ‘inter-mediate’) results. . . “ (p. 54).

This paragraph is crucial. When I read it the first time, and when I read it now, its meaning seems to me clear: PSA (psychoanalysis) in the MPRP operates as described in quotes, and the same for SEP (psychotherapy). But then, I remembered that Wallerstein (1985) wrote of this difference that "the postulated distinctive therapeutic modalities of psychoanalysis and analytically informed and guided expressive and supportive psychotherapies hardly exist in anywhere near pure or ideal form in the real world of actual clinical practice; that real psychoanalytic treatments in actual practice are inextricably intermingled blends of more or less expressive-interpretive and more or less supportive-stabilizing elements...". According to Wallerstein, the postulated distinction between PSA and SEP was hardly found operating in the MPRP. How come then that in B&S paper we read that in MPRP we find operating the very ideal distinction that Wallerstein clearly warns us is missing in practice? I had a straightforward way to solve the puzzle: to consult my cherished copy of "Forty-two Lives in Treatment" . I took it from the shelf and, believe it or not, I opened it at stroke at page 54 (out of 784 pages). I read: "In briefest capsule, these basic assumptions about the theory of psychoanalytic therapy are as follows: 1. Psychoanalysis operates essentially through...". (These lines are underlined in my copy, but I had forgotten this passage after twenty years). That is, it is true that  Wallerstein gives the definitions above of how PSA and SEP work (correctly quoted by B&S)--but this is not how PSA and SEP really operate in MPRP, it is only the *assumption* of how they operate--an assumption that was falsified by the research.

To make things even clearer, I reviewed other parts of the text that I had underlined two decades ago. Of the 22 cases (out of 42) originally in psychoanalysis, 12 were modified or converted in psychotherapy. Of the 10 cases of psychoanalysis non modified, only two rated "very good"--by far the worst result of all the groups. One of these two, the Tantrum Woman, is specially interesting, because it had, according to the patient, a turning point that decided of the successful treatment: "for the first year and a half I didn't feel I was getting anywhere. At the time he [the analyst] started yelling back, that was the first big turning point. He said 'Shut up'. I needed someone to shut me up. I needed it then...Before that I was running wild and he was letting me. Now I felt there was someone who would help me and not let me run wild...someone was there who was interested" (p. 179). This was one of the only two successful 'pure' analyses. All in all, I would say that if anything the MPRP demonstrates that psychotherapy is definitely *better* than psychoanalysis, if we accept the definitions given in the assumptions at page 54. But even this conclusion in my view would be trivial, because those assumptions are to me a matter of no relevance, a merely parochial question.  As I said, the really relevant points in my view are others. But before coming to these (in a next post, if I will be allowed), I have to terminate this case.

B&S found, through a re-elaboration of the MPRP data, and especially through new methods of evaluating Rorschach protocols, that there was a significant difference between the PSA and the SEP groups, if the dichotomy anaclitic/introjective was taken into account. They ascribe this difference to the different modes of operating of PSA and SEP, but this explanation is, as we have seen, faulty. The difference between the two approaches exists ideally only in the assumptions of the research, not in real treatments. The false attribution has been possible because the authors have mistaken the assumptions for the real modes of operating of PSA and SEP. Possibly, the difference pointed out between anaclitic and introjective patients is to be traced to the only real difference between the two groups: 4-5  versus 2-3  sessions per week, or the couch vs. face-to-face. Be it as it may, the bottom line is that a result favorable to PSA, correcting another one embarrassing for PSA, has been obtained through the presentation of the assumptions of the research as they were the real modes of operating of the two compared approaches. That is through a distortion (obviously unintentional) of the data. This is how the researcher allegiance works, and this is why, in my view, most clinicians are not very interested in empirical research.

But I want to confirm my esteem to Sid, in spite of this mishap (as I see it: please correct me if I am wrong). His emphasis on the two basic functions operating in all therapies, and his awareness that the Dodo bird verdict  is forcing  psychotherapy research to change its focus (but also its whole conception, I would add) is the ground where we can meet, in case he is interested.

Tullio Carere, September 24, 2007

I mistakenly substituted a preliminary version of the Westen paper for the final one. The preliminary unpublished version is Westen & Morrison, 2000. How empirically valid are empirically validated therapies? A critical appraisal [W1]. The final version is Westen D., Morrison K. &Thompson-Brenner H., 2004.The empirical status of empirically supported psychotherapies: assumptions, findings, andreporting in controlled clinical trials [W2]. I apologize. A wrong information received by an otherwise reliable source, according to which W2 was superposable to W1 for the points in question, made me quote in my previous posts W1 instead of W2 (at that moment I had only W1 at hand). The mistake, however, is an occasion for an interesting comparison of the two texts. Here are, firstly, the passages from W1:

"Summary:  The Assumptions of EVTs are Neither Theory-Neutral nor Empirically Validated

Two things about the assumptions underlying EVTs are striking.  First, they are not theory-neutral. In every case they are fundamental assumptions of cognitive-behavioral therapy, or at least the cognitive-behavioral therapy of the late 1970s, when these assumptions began to define what was considered a scientifically valid outcome study and hence to influence publication and funding decisions.  In virtually every instance they are the direct opposite of the assumptions of psychodynamic and many other forms of psychotherapy.  Second, most of these assumptions are empirically testable, and many of them have either never been adequately tested or have been empirically falsified to one degree or another."

"In many respects, this alternative approach represents a break with the Popperian philosophy of science that guides most psychological research—including psychotherapy research—in a way that extends, rather than limits, the scope of scientific method. Popper (1971) endorsed a distinction between two contexts of science:  a context of discovery, in which theories are crafted and hypotheses are generated; and a context of justification, in which hypotheses are tested and either corroborated (tentatively accepted) or disconfirmed.  According to Popper, the essence of science lies in hypothesis testing (justification). How we come up with our hypotheses, he argued, is our own business. "

In W2 the first paragraph disappears completely, and what remains of the second is  the following:

"This example highlights the extent to which the conclusions reached in the EST literature depend on a highly problematic tenet of Popper's (1934) philosophy of science that as a field we have implicitly embraced:  that the essence of science lies in hypothesis testing (the context of scientific justification), and that where one finds one's hypotheses (the context of discovery) is one's own business.  There can be no more powerful way to create a gulf between clinical practice and research than to compare laboratory-derived interventions with everything but what clinicians practice in the community."

My question is: What happened to the first paragraph? Of course many parts of a preliminary version of a paper are usually modified or canceled. But why just that paragraph that was particularly significant to me was canceled? My impression is that the cancellation is part of a general softening of the tones in W2, with the mitigation or elimination of those passages that could have hurt the community of the researchers, and pleased guys like me, critical of empirical research. But there may be more to it. The concept of theory-neutrality could be specially disturbing for those who believe that all observations are theory-laden. Theory neutrality not only challenges the Popperian philosophy of science (that in W2 remains "highly problematic", though the "break" has disappeared), but also presupposes the capacity and the will to suspend or bracket out all theories that is the hallmark of phenomenology--in contrast to empirical science. Clearly Westen did not want to go so far, and reframed the paper in a more orthodox style.

My general impression remains anyway that according to Westen et al a deep rethinking of the research on empirically supported treatments is necessary, reevaluating the context of discovery in the first place.  I agree with them, and with LB&C for that matter, that the research in this context should become a scientific venture in its own right--though of course, as I said, my idea of what would make the work in this context scientific differs substantially from both Westen's and LB&C.

Tullio Carere, September 25, 2007

I have a couple more of reflections on the Westen paper, intertwined with my response to Blatt's response to me. The first is on the paragraph disappeared in the final version of the paper. It is not a paragraph like any other. It is the summary of the first part of the article, featuring two "striking" conclusions, the first and more emphasized of which regards the non neutrality of the assumptions underlying EVTs, inasmuch as they are fundamental assumptions of cognitive-behavioral therapy. This is the very gist of the study, the  premise to the proposal of a "break" with the Popperian philosophy of science, in order to focus on the context of discovery that is to become a scientific venture in its own right, and not just a source of hypotheses. The question is: how come that a "striking" conclusion, the very core of the preliminary version of the paper, becomes a non existing matter in the final version? My hypothesis is that Westen realized that the field is not ready to a real break with the Popperian philosophy of science (or maybe he himself was not quite ready). In any case he prepared with his collaborators a final, politically correct version of the paper, one which would not disturb the empirical researchers with any disquieting hint to theoretical neutrality.

Blatt says that theories cannot be discarded (I agree: they should just be suspended), and in any case I myself am not theory free. In fact he is sorry that their findings upset my "assumptions and strongly held beliefs (theoretical commitments) about the lack of difference between psychoanalysis and psychotherapy". I am not sure where in my posts Blatt uncovered such beliefs of mine. What I think and said is that the difference (or lack of) between psychoanalysis and psychotherapy is to me just a matter of no relevance. The minimal condition for a difference to exist between one thing and anything else is the existence of that thing, and this can no longer be said of psychoanalysis. *One* psychoanalysis does not exist any more, what exists is *many* psychoanalyses. What is psychoanalysis to one school or group is psychotherapy to another, the one's gold being the other's copper. Of course to settle the question one can recur to institutional definitions. This is where an impossible question becomes a parochial one. My time is too precious to waste it in trivial or parochial questions--it is not a matter of beliefs or theories.

Of course I have theories, but my theories are not Blatt's theories. Maybe Gadamer (aptly evoked by Corbett Williams) can help us to understand each other. The Greek theoria is a mode "of being present in self-forgetfulness, and to be a spectator consists in giving oneself in self-forgetfulness to what one is watching. Here self-forgetfulness is anything but a privative condition, for it arises from devoting one's full attention to the matter at hand, and this is the spectator's own positive accomplishment" (Truth and method, p.126). "Our starting point is that verbally constituted experience of the world expresses not what is present-at-hand, that which is calculated or measured, but what exists, what man recognizes as existent and significant. The process of understanding practiced in the moral sciences can recognize itself in this--and not in the methodological ideal of rational construction that dominates modern mathematically based natural science" ( p.456). One can see in phenomenological observation or in Bion's attitude of listening without memory and desire the modern heirs of the Greek theoria. To avoid confusion between the two meanings of the word, one can call meta-theory what one sees thanks to the bracketing of all theories (in the ordinary meaning of the word). The 'validation' of metatheories happens not through measurements and experiments but through dialogue and confrontation among observers who are capable of and willing to suspend their idiosyncratic theories, in a spirit of "self-forgetfulness". This is what theory-neutrality properly means to me. In my view only a research based on this theory-neutrality can bridge the gap between clinicians and researchers. I can't see how a research based on measurement and statistics can ever bridge the gap that it has itself created.

Tullio Carere, September 26, 2007

Both versions of the Westen paper begin with the same sentence: "Robert Abelson (1995), [a leading psychological statistician], has argued that the function of statistics is not to display 'the facts' but to tell a coherent story – to make a principled argument." But in the final version the following disappears: "By this he does not mean that statistics can or should be ignored, distorted, or manipulated.  Rather, his point is that the purpose of reporting the results of sophisticated statistical procedures in scientific publications is to make a compelling case for or against a theory or hypothesis. Those of us who conduct research are certainly aware of the scientifically and ethically appropriate, inappropriate, and borderline ways of tweaking statistics to make such a case.  (...)  What is often less appreciated, however, is just how much storytelling is involved in deciding where to put the commas, parentheticals, 'buts,' and asterisks in scientific publications after the data have been appropriately analyzed.  This article is about what can happen when some of these rhetorical devices are inverted." It's a pity that this part has disappeared, because it sheds some light on the Blatter and Shahar paper.

As I noted earlier, in the B&S paper the point of insertion of the quotation mark made a considerable difference. To change «these basic assumptions about the theory of psychoanalytic therapy are as follows: 1. Psychoanalysis operates essentially through...» into «Wallerstein (1986) described PSA in the MPRP as operating "essentially through...» means to tell another story. What in one story are assumptions, in the other are operations. In the new story, thanks to the punctuation device, B&S can quietly ignore the fact that according to Wallerstein between the assumptions of how PSA and SEP work and what really happened in the two groups there was a huge gap, to the point that the postulated distinctions were hardly recognizable in real practice. At the minimum, to whipe away the enormous and extremely accurate work of Wallerstein with a quotation mark is unfair. But according to Blatt all that work could be left aside, in front of the fact that "most, if not all, of the analyses in the MPRP were conducted by candidates under supervision as part of their psychoanalytic training". It means that the supervision of candidates is considered a sufficient guarantee that all psychoanalytic treatments were conducted in a way that satisfies the assumption. Is the supervision of candidates really such guarantee? I would hardly say so.

The assumption is that PSA "operates essentially through the establishment of a full-fledged regressive transference neurosis, and its ultimate resolution comes about centrally

through interpretation leading to insight and mastery", whereas SEP is "similar to psychoanalysis in mechanism but differs sharply in degree." If we consider again the example of the Tantrum Woman, one of the only two "very good" results in the PSA non modified group, and read the extensive description of the case in Wallerstein (1986), we learn that at the conclusion of the first analysis, after almost five years, nothing like an "ultimate resolution" through interpretation of a full-fledged regressive transference had occurred, but just a "transference shift...not analyzed to resolution"  (a transference cure, in fact) that lasted less than two years, followed by the full return of the symptoms. The patient returned for a "reanalysis" at reduced frequency, for which no follow-up is available. One would fairly say that in this (as basically in all other) case just the criteria for a SEP, not a PSA, are met. If one examines the clinical material of the MPRP, one cannot but agree with Wallerstein that the distinction between PSA and SEP is hardly perceivable, the supervision of the candidates notwithstanding. If we nevertheless want to compare the two groups, we should take into account the fact that in the end of the 22 "psychoanalyses proper" only 10 were left, because 12 were modified or converted in psychotherapy. In the 10 left, there were 2 "very good" outcomes, that is 20 per cent. In all the other groups together (SEP plus PSA modified or converted in psychotherapy), 32 in all, there were 15 "very good" outcomes, that is 48 per cent. If we want to play the statistical game, which is not my game, PSA is no match for SEP in the MPRP. Wallerstein was very generous saying that the match ended all square (if we want to speak in terms of real therapy and real life--but may be in terms of ink-blot reading things are different).

The claim that the supervision of candidates is a guarantee for all PSA treatments to be conducted in a way that satisfies the assumption, or even to be more "interpretative" than the SEP treatments, is just begging the question, not a "fact" that one can find in the material. This confirms Abelson's argument: the function of statistics is not to display 'the facts' but to tell a coherent story – i.e. to make a compelling case for or against a theory or hypothesis. And, as Westen and Morrison point out in the politically incorrect version of their paper, an asterisk or a quotation mark are rhetoric devices that can serve to tell very different stories. My conclusion: I fully agree with LB&C on the importance of minding and trying to bridge the gap between clinicians and researchers. But I fully disagree that there is a bridge to build between hermeneutics and quantitative research, for the simple reason that  statistics (at least in our field) are nothing but (or little more than) just another form of hermeneutics (or perhaps of rhetoric). And I prefer the hermeneuts that call themselves hermeneuts, than those whot disguise their hermeneutics under sheets of numbers.

Tullio Carere, September 29, 2007

Blatt is not sure what I disagree with in his and Shahar's further analyses of data from the MPRP. I am not sure what was not clear in my disagreement, but will try anyway to make my argument clearer.

1. B&S's further analyses are based on the assumption that the criteria for differentiating the two types of treatment are reasonably certain. But their certainty is based only on the transformation, through a rhetoric punctuation device, of the *assumptions* of the MPRP on how psychoanalysis, expressive and supportive psychotherapy are supposed to work, into the way the treatments were *really* conducted. The most striking--and, to many, disappointing--result of the MPRP was that those assumptions were fully disconfirmed by the data. I quoted the case of the Tantrum Woman, because it was one of the only two cases of "psychoanalysis proper" ( i.e., non modified or transformed in psychotherapy) whose outcome was rated "very good". At the end of a five-year analysis, it was very clear that the symptomatic cure had to be ascribed to mechanisms like corrective emotional experience, transference cure, identification with the therapist--in other words, it did not even meet the criteria for an expressive, but just for a supportive psychotherapy (after two years the patient totally relapsed and was followed for four more years in a "reanalysis" at reduced frequency that met the criteria for an expressive psychotherapy,  whose result is however dubious because the patient disappeared, denying herself to a follow-up). It is obvious that this treatment was not a "psychoanalysis" (as defined by the MPRP assumptions)--letting alone a "very good" one-- but just a supportive psychotherapy, probably a little more expressive in the second round. At very similar conclusions one can easily arrive examining the available material for all other cases.

2. To the shaykh Elish el-Kebir is ascribed the saying: " If the Christians have the sign of the cross, the Muslims have the doctrine of it". The kernel of the doctrine is that the universe is formed by two dimensions, the horizontal and the vertical, nature and spirit. In fact this symbolism is widespread in all cultures. Pianist Helene Grimaud said of Beethoven: "His music has a strong philosophical dimension, but is in the same time deeply rooted in the earth, in human nature with all its frailties, troubles and weaknesses. There always is in him a search of absolute, an attempt at reconciliation of the vertical and horizontal dimensions of existence." My interest in the Topeka research was mainly due to the fact that I saw the two dimensions, there called supportive and expressive, operating in all treatments, independently of how they were labeled--psychoanalysis or psychotherapy (by the way, Blatt too is persuaded of the centrality of these two dimensions in all psychological-existential processes--I hope that on this common ground we shall still be able to meet, once our irreconcilable differences are clarified). Horizontal-supportive and vertical-expressive elements were inextricably intertwined in all therapies. The specific combination of these elements was determined by the process developing moment by moment between patient and therapist, not by the form of treatment chosen by the therapist. Although candidates were strongly motivated by their training to work in a classic analytic mode, as defined by the assumptions of the research, their motivation was far too weak in comparison to the thrust of the process, to the point that in the material collected by the researchers the assumption that psychoanalysis should be deeper or more "vertical" than psychotherapy was totally disconfirmed.

3. Luyten wrote: "in contrast to what has been suggested by some in this discussion, data are often stubborn and simply refuse to confirm our cherished beliefs." Right, the data of the MPRP are stubborn and refuse to confirm the cherished belief for "psychoanalysis" to be deeper or more vertical than "psychotherapy", as this difference is usually (and in particular in the MPRP) conceptualized. According to Blatt, "the supervision of the treatment provided by the candidates essentially monitored the adherence to psychoanalytic treatment as defined at the Menninger Clinic at that time." I pointed out that this is just begging the question, nothing to do with the available data. If it were true that such monitoring took place, the supervisors should have taken cognizance of the fact that not one of the forty-two treatments supervised adhered to the criteria for psychoanalytic treatment as defined at the Menninger Clinic at that time. This would have meant to acknowledge that "psychoanalytic treatment" was a myth existing in the mind of the psychoanalysts, not in real practice with real patients (not candidate-patients)--with the implication that the whole building of psychoanalytic training was just an institutional device aimed at supporting a collective form of wishful thinking (the "trainer allegiance" being the equivalent of researcher allegiance for training). It is understandable that the supervisors did not want to wake themselves and their supervisees up from their shared dream, but this could not prevent the production of written materials from the treatments at hand that totally disconfirmed the myth. Finally, the Blatt and Shahar's further analysis of data from the MPRP is in itself a datum that confirms Abelson's argument that the function of statistics is not to display 'the facts' but to tell a coherent story--in other words, it is a form of hermeneutics that conceals its hermeneutic nature under the pretence of being solid science, supported by an inordinate and in my view unwarranted use of the methods of natural sciences (experiments and quantitative measurements).

Tullio Carere, October 4, 2007          

I summarize some of the more (to me) relevant points in the current debate.

1.  As Zvi tellingly puts it, “Blatt, Luyten and Corveleyn are notpositivistic: they are hermeneutic from the get go”. In an analysis ofBlatt & Shahar’s 2004 paper, I observed that their positivism is justa facade for a (weak) form of hermeneutics, to the extent thatstatistics and rhetoric devices are used not to display facts, but tosupport the story they want to tell.

2.  In a hermeneutical perspective, as presented by Irwing Hoffman, theanalytic relationship is assimilable to a text, the meaning of anyword or act of which is discovered or made in the context in which itis said or done. Every meaning is contextual and co-constructed, butconstructions are not arbitrary: some are good, others are not so good(no analyst maintains that anything goes). The question is: how do weassess the goodness of a construction (or interpretation, orintervention)? As I. Hoffman warns, this is not just a scientificquestion—it also involves ethic and aesthetic considerations.

3.  Firstly, to say or do the right thing at the right moment belongsto the art, more than to the science of therapy, insofar as itrequires an intuitive appreciation of the context in which one moves.  Only to the extent that the analyst is free of any prejudice andexpectation, or the mechanical application of any scheme, can s/herespond creatively to the situation on a moment by moment basis. Agood therapy requires first of all an analyst who is free ofpreconceptions, capable of following their intuitions andinspirations, spontaneous and natural. The hermeneutic sidecorresponds to the art of therapy. If we want to understand whatscience means for psychotherapy, we should not forget that herescience is one side of a coin that has art on the other.

4.  Real therapy is the product of the creative and largelyunforeseeable co-construction and co-discovery by both patient andtherapist, not the administration of empirically validated procedures(which would only stifle spontaneity and creativity). On the otherhand, it also stands to reason that the more knowledgeable thetherapist is about the basic patterns of the field, the more effectivetheir work is likely to be. For instance, it is obvious that theidentification of defences is easier if the clinician is knowledgeableabout the more common defensive patterns, horizontal and verticalsplitting, etc. The therapist should be familiar with as many patternsof the field as possible, and be able to use them when indicated inthe most flexible and customized way—as they should also be able toset aside any pattern and work creatively to respond to the demands ofthe unique encounter with their patients.

5.  A general science of psychoanalysis, or psychotherapy (the use ofthe two words as interchangeable is consistent with the results—sofar unchallenged—of the Menninger Psychotherapy Research Project)would consist of the systematic description of the basic patterns, orinvariances, or regularities of the field—more or less as in botanyor zoology. The development of this science has been hampered so farby the theoretical orientation of the field (every school orresearcher being rooted in their own theoretic allegiance), whereasthis science requires a meta-theoretical attitude: the suspension ofany theoretical allegiance that allows the study of the phenomena ofthe field, independently of the therapist’s theoretic persuasion. Thestudy of the common ground, common factors, or common patterns of thefield is made possible by a meta-theoretical (or phenomenological)attitude, not by an empirical approach, which can only validate orinvalidate individual theories.

6.  The therapist is an artist, to the extent that they interpretcreatively the general science of psychotherapy in order to apply itto the individual case. But then they are again a scientist, a localscientist, to the extent that they monitor all the time the effects ofwhatever they say or do in the therapeutic relationship, and correctin real time their movements as a function of the feed-backs theyreceive. The therapeutic setting, beside being an atelier or a scenewhere various scripts are represented, deconstructed andreconstructed, is also a scientific laboratory, where all sorts ofhypotheses are formulated and put to test in the therapeuticrelationship and everyday life, and even experiments are undertaken, in order to make discoveries or test hypotheses.

7.  In conclusion, a general, metatheoretical science, coupled with a local science, fits in well and aptly integrates with the basically hermeneutic, contextual, creative nature of the psychoanalytic/psychotherapeutic enterprise, whereas empirical-statistical research is felt by most practitioners as something fundamentally alien to their practice.

Tullio Carere, October 7, 2007          

I have never met Blatt in person, but I have an image of him as a kind and friendly guy. When I asked him to send me a paper, he sent me two. In the same time, and in some sharp contrast, I see in him the perfect illustration of the empirical mind at work. Let me summarize the evidence for my statement.

In my analysis of the Blatt and Shahar's 2004 paper I have shown in a way that has seemed to me indisputable--and in any case has not been disputed by Blatt--that the author's certainty [that the criteria for differentiating the two or three types of treatment are reasonably certain] is based only on the transformation, through a rhetoric punctuation device, of the *assumptions* of the MPRP on how psychoanalysis, expressive and supportive psychotherapy are supposed to work, into the way the treatments were *really* conducted. In fact, the data produced by this research, which can be extensively consulted in Wallerstein's 1986 "Forty-two lives in treatment", fully disconfirm the assumptions of the Project. Not one of the forty-two cases met the presumptive criteria for "psychoanalysis proper", no significant difference was found between the three or two groups, as regards both the technique and the "depth" of the treatment, and the treatment outcome (with one exception: the cases initially labeled as "psychoanalysis proper" had in general the worse outcomes).

As I said, Blatt did not dispute this evidence, but  just ignored it, in favor of his hypothesis that "the supervision of the treatment provided by the candidates essentially monitored the adherence to psychoanalytic treatment as defined at the Menninger Clinic at that time." I pointed out that this is mere begging the question, and has nothing to do with the available data. Although candidates were strongly motivated by their training to work in a classic analytic mode, as defined by the assumptions of the research, their motivation was far too weak in comparison to the thrust of the process, to the point that in the material collected by the researchers the assumption that psychoanalysis should be deeper or more "vertical" than psychotherapy was totally disconfirmed. The idea that the treatments of one group were more "interpretative" and the others more "relational" is to be found in Blatt's mind, or in Blatt's faith, not in the research material.

But Blatt insists: he does not discuss the evidence that I lay out, but dismisses it as just a product of my "belief" that there is no difference between psychoanalysis and psychotherapy. So, my evidence is dismissed as my belief, his belief is prodigiously transformed into evidence! This seems to me a perfect example of the rhetorical devices of the empirical mind at work. But let us examine Blatt's actual evidence. In his further analysis of the data of MPRP, which employed "new methods for evaluating Rorschach protocols", he did find some differences between the two groups that were labeled as psychoanalysis and supportive-expressive psychotherapy. I don't dispute his evidence--my competence with Rorschach protocols is not good enough for that. Maybe there were after all some differences between the two groups, differences that the clinical material did not record, but ink-blot reading did. Why not? It is possible. But let us take these differences for granted. What do these differences suggest? Do they suggest, as Blatt does, that they reflect "a difference between an emphasis on interpretative vs. relational elements in the two treatments, and that these two elements of the treatment process may have had important differential effects of two types of patients (anaclitic and introjective)"? Yes, if we stubbornly choose to believe that a difference between an emphasis on interpretative vs. relational elements in the two treatments did exist in MPRP, in spite of all the evidence to the contrary. It is true that in 10 out of the initial 22 "psychoanalytic" cases "the analyst endeavored to maintain the classical analytical situation unaltered within the analytic hours" (Wallerstein, p 186). But if we consider the difference between psychoanalysis proper and expressive psychotherapy, as laid out in the assumptions of the Project (p. 55), we learn that the two forms of treatments are similar in mechanism, but "differ sharply in degree". Expressive psychotherapy "is limited in focus to agreed-upon sectors of psychic distress and personality dysfunction, and operates through means that do not evoke a full transference regression, all leading to less extensive (more 'intermediate') results but similar in direction and kind". Now, this difference--the only difference between the two forms of treatment--is nowhere to be found in the real practice even of those 10 cases so optimistically labeled "psychoanalysis proper", as Wallerstein honestly recognized. It means, if we want to leave aside any belief and just rely on normal logic and common sense, that the 10 analysts did endeavor to maintain a classical analytic situation, but their endeavor was completely frustrated by the inner logic of the process, with the result that the presumptive differences were completely absent in real practice.

If we want to remain true to the evidence, leaving aside questions of faith, Blatt's suggestion does not hold, but we can consider more reasonable suggestions. Firstly, an actual difference between the two forms of treatments did exist: the frequency of the sessions. Simply put, the patients of one group received more sessions than those of the second. This did not make for significant differences in outcome (if we want to be generous, because in fact the patients of the "psychoanalytic" group had worse outcomes on average), but it did make for differences in ink-blot reading, which could speak for some inner change that was not apparent at the clinical level. This suggestion would be similar to the one of the researchers of the Stockholm STOPP study cited by Luyten, that the observed differences (between "psychoanalysis" and "psychotherapy") depend on the duration of treatment.

A second suggestion is connected to Blatt's hypothesis that the introduction of relational and intersubjective approaches to psychoanalytic practice might "muddy the waters between these two fundamental elements of the psychoanalytic treatment process (interpretative and

relational)". I do not think that this is the case, for the reason that the waters have always been muddy--the MPRP being a most clear evidence for this muddiness, long before the introduction of relational and intersubjective approaches. It seems to me that is only the dominance of the golden myth of psychoanalysis that has prevented so far those in need of that myth from seeing the muddiness that has always been there. The therapeutic encounter has been "sloppy", co-created, ambiguous and unpredictable all along (Stern, The present moment, 2004).

Finally, I want to respond to the charge that I use the data of research only when they confirm my beliefs. As I hope it will be clear by now, I am not at all against research. I only object to empirical or theoretical research, i.e. that sort of research aimed at testing hypotheses or theories--which is most appropriate in the hard, not in the human sciences--but am very much in favor of observational or meta-theoretical research. Above all, I am very much against the scientistic ideology, according to which only hypothesis testing through the collection of repeatable and measurable data deserves the name of scientific research. I, like most clinicians, make little, if any, use of that kind of research, but have no doubt about the decisive importance of observational research--the one, by the way, to which we owe the very existence and development of psychoanalysis. In this line, we could (I would say we should) recover Freud's Junktim, that the current empirical emphasis of research has made a little outmoded. In this perspective, every clinician is, could or should be, a researcher, taking back this responsibility from the hands of professional researchers. In my view the bridge to build is not, as LB&C maintain, the one between hermeneutics and empirical research, either because the latter is just, as I and others suspect, a disguised and weak form of hermeneutics, or because it has a positivistic approach that is incompatible with the essence of psychoanalysis. The bridge to build, or the integration to make, is rather the one between hermeneutics and phenomenology, for a style of work that is respectful of the insuperably contextual, floppy, co-creative and co-constructive nature of the psychoanalytic encounter, and in the same time is knowledgable of the invariances or regularities or common factors or common ground of the field, which become the more plain and discernible, the more one is free of theoretical presuppositions and expectations.

Tullio Carere, October 7, 2007

I thank Patrick Luyten for the opportunity he gives me to clarify my position with his remarks.

First of all, I want to reiterate that I have nothing against science, but much against scientism, an ideology based on the obsession with repeatable and measurable data, and on the pretence that there is no science outside this obsession, and no valid knowledge outside this science--with the implication that all other forms of knowledge are at best sources of hypotheses to validate through empirical testing. For the field of psychotherapy, this ideology tends to blur the borders that separate this discipline from medicine, furthering the current medicalization of psychotherapy--which is to me a most unfortunate event.

According to Luyten, my "own comments betray a strong self-confirming bias, and a reliance on subjective judgments whenever they confirm cherished theoretical views, but not when they disconfirm them, and similarly, research findings are cited to confirm cherished viewpoints, but are considered as totally invalid when they disconfirm them." He offers some examples of what he sees as my "self-confirming bias":

1. Luyten writes that I disregard "the extensive empirical evidence documenting that the therapeutic setting should not be used to test hypotheses and justify knowledge". The empirical evidence cited by Luyten documents that the therapeutic setting should not be used to test hypotheses and justify  *non-contextual* knowledge, but has nothing to do with *contextual* knowledge, which is the one I referred to in the passage that Luyten criticizes. Psychoanalysis is fundamentally contextual and co-constructive, but constructions are not arbitrary, inasmuch as there are good and less good constructions. For psychoanalysis to work, it is necessary for the analyst to have the possibility to test the goodness of constructions or interpretations *inside the therapeutic setting*. And because goodness does not only have ethic and aesthetic sides, but also has a critical connection with truth, it is mandatory for the analyst to be able to test their contextual hypotheses inside the setting, unless they decide that psychoanalysis as such has nothing to do with truth, or all questions of truth are delegated to empirical researchers--both decisions being obviously lethal for psychoanalysis.

2. Luyten: "If one strongly believes that there are no differences [between psychoanalysis and psychotherapy], as Carere apparently does, one sees confirmation for this cherished belief everywhere." I wonder if Luyten read my previous post where I replied to the very same charge that Blatt brought against me. As it seems he didn't, I copy here from my September 25 post: << I am not sure where in my posts Blatt uncovered such beliefs of mine. What I think and said is that the difference (or lack of) between psychoanalysis and psychotherapy is to me just a matter of no relevance. The minimal condition for a difference to exist between one thing and anything else is the existence of that thing, and this can no longer be said of psychoanalysis. *One* psychoanalysis does not exist any more, what exists is *many* psychoanalyses. What is psychoanalysis to one school or group is psychotherapy to another, the one's gold being the other's copper. Of course to settle the question one can recur to institutional definitions. This is where an impossible question becomes a parochial one. My time is too precious to waste it in trivial or parochial questions--it is not a matter of beliefs or theories.>> Luyten then cites the Stockholm STOPP study, that suggests that these differences are related to the duration of treatment. If the difference between psychoanalysis and psychotherapy is to me a trivial question, the duration of treatment is not. Yet I think that it would be folly to rely on empirical research to decide the duration of a treatment, which is, as any other meaningful decision in the treatment, a contextual matter, depending on the patient's motivation, capacity, and goals, to say the least.

3. Luyten: "Note the statement: "I observed" and the far-reaching conclusion ("their positivism is a facade for weak hermeneutics"), and his conviction that this is a general trend of research (data are only a cover to tell a cherished story)." I quoted two general statements, the first by Zvi Lothane: "Blatt, Luyten and Corveleyn are not positivistic: they are hermeneutic from the get go". The second by Westen et al: "Robert Abelson (1995), [a leading psychological statistician], has argued that the function of statistics is not to display 'the facts' but to tell a coherent story – to make a principled argument." To Lothane and Abelson's general statements I added my observation that the way Blatt and Shahar conducted their further analysis of the data from the MPRP is a perfect examplification of Zvi's and Abelson's general statement. Blatt and Shahar's is to me a meaningful example, firstly because Blatt is one of the authors of the paper in discussion, secondly because it is repeatedly quoted by LB&C as a prominent piece of research. Therefore it seems to me legitimate to say that B&S's paper is in itself a case that corroborates Lothane's, Abelson's, and my general impression. It is just a strong corroboration, nothing more and nothing less.

4. Luyten: "Although some of our cherished hypotheses have been confirmed, there are many that are not, and no matter how hard one should try, they clearly contradicted our cherished theory." I agree. I definitely admitted in a previous post that, once discounted the researchers allegiance, there remains a minor part of valid results. But, I added, the question is that most of these results look trivial to most clinicians, i.e, they are seen as hardly relevant to practice, or just confirming common-sense conclusions. I appreciate Luyten's modesty, in admitting that their results are "very modest at best actually"--but I think that the triviality or modesty of most results of empirical research is not contingent, or bound to change for the better as a result of a systematic application of what Luyten calls the "empirical cycle - theory -hypotheses - results - feedback to theory - new hypotheses and so on". Hypothesis testing is appropriate at the local level, with contextual hypotheses, but it hardly is so at a general level, for the study of the invariances or regularities of the field, because of the insurmountably contextual and co-constructive nature of psychoanalysis. By definition, a method devised for the verification/falsification of theories is not appropriate for the study of what happens independently of the therapist's--and the researcher's-- theories. At this level what is required is not a theoretical, but a metatheoretical ( i.e. phenomenological) approach. And this  level is, according to the Dodo bird, the most significant for psychoanalysis/psychotherapy, the one to which we should begin to devote our best energies.

5. Finally, Luyten thinks that his own approach "does much more justice to the complex reality and is much more fruitful than solely relying on subjectivity and the artificial splitting of theory and research". I don't see my approach as "splitting" anything. I only distinguish theory from meta-theory (which corresponds to the Greek "theoria"), as empirical from transcendental subjectivity, or theory-laden from theory-neutral observation. Both are legitimate, but the former (the empirical, quantitative, theory-laden approach) is bound in my view to produce in our field only marginal data, of little use for the clinicians. Luyten adds that "the danger of this hierarchical view is that one is prone to disregarding evidence that contradicts cherished assumptions, which Carere's comments clearly illustrate". I have failed to see this clear illustration in Luyten comments to mine. To the contrary, it seems to me that it is the empirical approach that is "prone to disregarding evidence that contradicts cherished assumptions", as I think will be clear in my further analysis of Blatt's position that I am posting together with this comment.

In conclusion, I have examined all instances of my "self-confirming bias", but have failed to find what Luyten has found. I suspect that my failure in seeing my self-confirming bias will be seen by Luyten as a confirmation of the same self-confirming bias. Nevertheless, this exchange is very fruitful to me, and I hope it will be a little so to Luyten too, and to some of those who have had the patience to follow us so far.

Tullio Carere, October 9, 2007

Some have noticed, as Hoffman himself did, that my ideas on the hermeneutic quality of the psychoanalytic relationship are very much the same as his.  We both see it as basically contextual, ambiguous, co-creative and co-constructive. I also very much agree with his emphasis on the patient’s agency and responsible contribution to the process, in a way that goes beyond the current relational paradigm.  Furthermore, my consonance with him goes over hermeneutics, to a broad dialectical attitude that aims at correcting the many dichotomies and one-sidednesses of the field—particularly in regard to the polarities spontaneity/ritual and personal/technical interaction. But right here, on the dialectical ground, I begin to miss something. I would have expected a more dialectical attitude about the one-person/two-person polarity, instead of a plain bias for the two-person. In his 2006 IJPA paper (The myths of free association) he quotes Bollas’ 2002 booklet “Free association”: “The analyst is left with Freudian faith: a belief that if one gets rid of oneself (and all of one’s theories) and surrenders to one’s own emotional experiences, then eventually the patient’s unconscious thought will reveal itself”. I am a little surprised that Hoffman does not mention here the even more radical Bion’s stance of “freedom from memory and desire”. Anyway, Hoffman criticizes  Bollas’ “Freudian faith” with the Macalpine argument that the standard Freudian stance does not merely create the conditions for spontaneous self-expression through free association, but amounts instead to a form of deprivation with powerful influence on the patient’s experience. A more balanced position would be that the Freudian stance can indeed be experienced by the patient as a form of deprivation, but not necessarily so. The analyst can, and in my view should, dialectically oscillate between a position of deep personal involvement, that allows for the patient to have vital relational experiences, and one of self-effacement, well described by Bollas’ and Bion’s formulas. The latter position is not easy to obtain, and must be established “as a permanent, durable and continuous discipline” (Bion, Cogitations, 1970-1992). Only to the extent that such discipline (only implicit in Freud but made explicit by Bion) has been established, is one free from the opacities that obstruct intuition.  The more the analyst can approximate this freedom, “the more confidently can he discount the origin of his observations as due to the ‘personal equation’” (Bion, ibid.). To the extent that intuition is cleared from its opacities, by means of a special discipline that phenomenology calls epoche’ and Bion calls freedom from memory and desire, one gets to the basics of lived experience – or, in Husserl’s terms, one returns to the things themselves.

The dialectic between a hermeneutical and a phenomenological position extends far beyond the specific theme of free association: one can see its necessity against the danger of transforming the hermeneutic approach into some form of cultural costructionism, in which any idea of objective truth—and therefore of science—disappears. One can take any feature of the analytic process described by Hoffman, for instance the unconscious wisdom guiding many enactments. A positivist could ask: how do you know that such thing as an unconscious wisdom exists, in the first place?  How do you expect us to believe your description, if it is nothing but a construction of yours, a beautiful story that you and your patients tell to each other? Or do you claim that it is not just one of your infinite stories, but a truthful description of what really happens in the process? In this case, what is your evidence? Do you have anything better than an ordinary anecdotal evidence? Empirical research is there just for investigating the objective validity of the subjective experience of the analysts. If you reject empirical research as a way of giving scientific status to psychoanalysis, how do you hope to overcome the level of merely subjective experience?

That level can be overcome either in an empirical, or in a phenomenological direction, or in both. But once the basically contextual, ambiguous, co-creative and co-constructive nature of the psychoanalytic process has been realized, one also realizes that empirical research (that needs repeatable and measurable data) cannot be of much help here. Instead, one can easily observe a number of recurrent regularities in the however ambiguous and unpredictable psychoanalytic process. The phenomenological approach is the method for the rigorous study of those regularities. Given Hoffman’s hermeneutic and dialectical orientation, I would have expected a special, or rather central, consideration for the hermeneutic/phenomenological dialectic. I miss it in an otherwise wonderful work.

Tullio Carere, October 13, 2007

Robert White wrote: “I have come to think of the discussions as havingsimilarities to analytic process. If one attends closely to theevolving discussion, it is highly repetitive yet interesting detailsand new ideas can emerge slowly.” It has been my experience too.  Repetition is impolite in ordinary conversation, not in workingthrough conflicts. And there is a big conflict indeed to cope with, inthe theme of the article under discussion. A growing number ofanalysts share Horowitz’ view about “the difference between analysisand research. Research is outside the analytic envelope in its questfor a sober and objective (objective) pursuit of truth. A bunch ofresearchers could study an analyst and patient as an autopoietic dyad,but they would not include the analyst or the patient as parties tothe establishment of some sort or reliability and validity.”  Freud’sidea that psychoanalysis, beyond being a theory of the mind and amethod of treatment, also is a method of research in its own right, isconsidered today by many outmoded or plainly wrong. At the most,analysts can produce hypotheses, whose validity must be decided byempirical research. I see at the horizon, should this trenddefinitively obtain, a situation in which analysts hand their recordedsessions over to the researchers, who firstly check their compliancewith the guidelines established by research, and secondly examine therecorded material for producing new guidelines for the analysts tocomply with. A big brother scenario, as I see it.

Now for a final response to Luyten (those who are inconvenienced byrepetitions are advised to stop reading here). He asks: “ If these[the researcher allegiance and the Dodo bird verdict] are trivialfindings, how then can they be the core of Carere’s argument?”. As Irepeatedly said, most (not all) clinicians find that most (not all)results of empirical research are trivial, i.e. of little relevance topractice, or just confirming common-sense conclusions. The twoexamples made by Luyten are in fact trivial inasmuch as they confirmcommon-sense conclusions. The Dodo bird verdict is a metaphor createdby Rosenzweig (after Lewis Carrol) in 1936, for the phenomenon that hefirst, and many others after him, described—the phenomenon thatcommon factors account for most of the variance in psychotherapyoutcome. Much later this observation was corroborated by empiricalresearch, but this result is not trivial only to those who need toempirically justify even the most obvious observation, and are unableto find justification in the observation per se—in other words, tothe scientistic mind, which can only believe in statistics. (The samecan be said for the researcher allegiance: Popper himself observedthat it is all too easy to have one’s cherished theories verified byresearch, empirical or not—hence his well known emphasis onfalsification).

As for Luyten’s statement that “there is no empirical research without interpretation, and there should be no interpretation without empirical research”, I agree on the point that interpretation (or hermeneutics) is not enough—it must be complemented by something else on the side of objective truth. I would modify his sentence into thefollowing: “there is no phenomenological observation withoutinterpretation, and there should be no interpretation withoutphenomenological observation”. This, by the way, was Freud’s approach,although his phenomenology was only implicit, and his epoché far fromperfect. He thought and taught that this is the method ofpsychoanalytic research, and was quite clear in his refusal ofempirical research as basically useless to psychoanalysis. This is notto say that we have just to return to Freud, and nothing else isneeded. On one side Freud was even too much a phenomenologist, withhis optimistic faith in the analyst’s neutrality; on the other he wasnot enough a phenomenologist, with his reluctance to let go of hischerished theories. However, a more balanced dialectics betweenhermeneutics and phenomenology is on the way opened by Freud, arefinement of his method of research—whereas the assertion thatpsychoanalysis is just a source of hypotheses that must be validatedfrom the outside with statistical methods would make Freud turn overin the grave.

In any case, I am not going to stand on a giant’s shoulder in order tomake my case. Standing on my own feet is enough for answering thequestion: why do I say that the dialectic hermeneutics/phenomenology,and not empirical research, is the right method for the study of theregularities of the psychoanalytic/psychotherapeutic interaction?  Because the nature of the therapeutic interaction is such, thatphenomena of this field cannot be isolated, counted and summed as ifthey were bricks or potatoes. As Irwin Hoffman puts it, “Whenresearch findings are privileged so that they are given the ‘authority’ to dictate how certain patients with one or another traitor symptom should be treated, we slide into technical rationality, amode of practice that does violence to the complexity andconsequential uniqueness of our patients, of the two-person encounterin which we are engaged, and of specific moments within that two-person encounter.” The hermeneutic approach is respectful of theuniqueness of every therapeutic encounter, but it cannot account forthe regularities of the field: therefore it must be complemented by aphenomenological approach. This is neither the place, nor the time, toargue about a hermeneutic-phenomenological dialectic. Suffice to saythat two of the greatest thinkers of the 20th century, Freud andHeidegger, struggled for the foundation of a hermeneuticphenomenology—implicitly the former, explicitly the latter. I can’tsee another way to go, if we don’t want to surrender our autonomy tothe empirical researchers (who could anyway give some usefulcontribution to psychoanalysis, once their influence is aptlydownsized).

Tullio Carere, October 14, 2007

I had already bowed out, but I can’t resist getting back after readingIrwing Hoffman’s last post. After pointing up the “fundamental andirreducible ambiguity of the analyst’s behavior”, he firmly states hisbelief that a theory-free observation is not only impossible, but evento set it up as an ideal seems undesirable, “because impossible idealslend themselves to the cultivation of the illusion that they have beenachieved”. Finally he declares that “the idea that one can rid oneselfof any subjective bias and apprehend the ‘true’ nature of the object,that’s positivism at it’s most dangerous worst.”

My question is: How does Hoffman know that the ambiguity of theanalyst’s behavior is “fundamental and irreducible”? His statementsounds very definitive and non ambiguous. He speaks as one who knows,beyond any reasonable doubt, the true nature of the analyst’sbehavior. But is such a claim not “positivism at it’s most dangerousworst”? Yes, I agree: that’s a form of positivism, maybe a dangerousone. Inside the constructivist belief one can see a robust positivismin disguise (just as one can often see in empirical research a form ofhermeneutics in disguise).

No one—certainly not me—stated that the no-person position can bedefinitively or absolutely attained. Only dogmatic people believe thattruth can be the definitive property of a human being. This is not tosay that we cannot strive to direct our gaze on “the thingsthemselves” (Gadamer quoting Heidegger, in Truth and Method, p.  266-7), bracketing off all “arbitrary fancy” and “habits of thought”,anything that does not speak to us from “the things themselves”. In agenuine (neither empirical nor constructivist) form of hermeneuticsthere always is a phenomenological kern. There is a time-honoredtradition, from Plato to Husserl, from Freud to Bion, that one can(and must) bracket off, suspend, neutralize all subjectiveinterference, all ‘memory and desire’, all theoretical lenses in orderto devote as much as possible one’s attention to “the thingsthemselves”. Of course this suspension can never be perfect: it canonly be a “permanent, durable and continuous discipline” (Bion).  Besides, in the case of the analytic relationship, the “thing itself” can be the relationship itself (in the two-person perspective). Thismeans that the analyst must direct his attention to whatever happensin the relationship, moment by moment—yet always paying attention asmuch as possible to the process, not to their theories of the process.

This is also not to mean that theories are useless. To the contrary(sorry again, I repeat myself once more) I believe that the analystshould have many theories in their quiver, because they can be useful, maybe necessary for a preliminary understanding of the phenomena. But then they should also be able to suspend or step back from them all, in order to assess which of them, if any, can illuminate which part of the phenomenon at hand, and above all to look at things with fresh (as fresh as possible) eyes. Finally, the hermeneutic-phenomenological dialectic means at least that in the understanding of things we alternate between a discoursive-interpretive and an intuitive-contemplative attitude. This is what Aristotle called the noetic-dianoetic dialectic (but he warned that the intuitive-noetic was paramount, the discoursive-dianoetic being just auxiliary).