Werner Ulrich's Home Page:  Ulrich's Bimonthly

Formerly "Picture of the Month"

 

 

 

 

 

 

 

 

 

 

 

May-June 2017
If Systems Thinking is the Answer, What is the Question?
Discussions on Research Competence (Part 1/2)

   Ulrich's Bimonthly

 

 

 

 

 

 

 

 

 

Abstract  This essay originates in a seminar with research students and staff of the Lincoln School of Management in Lincoln, UK, as well as in countless discussions with students and professionals from many other fields, on the nature of research competence in the applied disciplines. The aim was to guide the participants towards reflection on their personal notion of competence as researchers and (future) professionals, especially as seen from a perspective of critical systems thinking. By expanding the original working paper and making it available publicly, the author hopes to reach a wider group of readers who seek orientation in formulating or advancing a research project, or who quite generally wish to clarify and develop their notions of good research practice and professional competence. The essay addresses readers in a direct and personal way.

 

Previous |

 Next

For a hyperlinked overview of all issues of "Ulrich's Bimonthly" and the previous "Picture of the Month" series, see the site map

PDF file

Note: With this and the next Bimonthly, I continue my plan of occasionally offering HTML versions of older publications of mine that so far have been available in PDF and/or hard print format only. I have revised and updated a working paper that dates back to my time at Lincoln University in England (1997-2000) and in which I report about a seminar on the nature of competent research as seen from a "systemic" perspective. As the new version has grown a bit long for a web page, I decided to split it up into two parts that appear in this and the next Bimonthly. The PDF version, however, offers an integral version of the full essay.

 

Essay history and suggested citation  The original article was circulated as Working Paper No. 22, Lincoln School of Management, University of Lincoln (formerly University of Lincolnshire & Humberside), Lincoln, UK, June 1998 (Ulrich, 1998a). A first, slightly amended online version (in PDF format only) was prepared for the author's Academia.edu site in April 2017 and was also made available in the Downloads section of the author's home page. A different, considerably expanded version of the original essay had previously appeared under the title "The quest for competence in systemic research and practice" in Systems Research and Behavioral Science, Vol. 18, No. 1, 2001, pp. 3-28 (Ulrich, 2001); but since this journal is not published in open-access mode, the article has to this date remained unavailable to a wider audience who has no access to the journal. Copyright conditions still do not allow me to offer that essay in my home page. The present, first-ever HTML version is a thoroughly revised, expanded and updated version of the April 2017 article, with some text passages that are entirely new, or different or missing, as compared to the earlier versions.

Suggested citation: Ulrich, W. (2017). If systems thinking is the answer, what is the question? Discussions on research competence. (Expanded and updated version of Working Paper No. 22, Lincoln School of Management, University of Lincoln, Lincoln, UK, 1998.) Ulrich's Bimonthly, May-June 2017 (Part 1/2) and July-August 2017 (Part 2/2).
[HTML] http://wulrich.com/bimonthly_may2017.html (Part 1/2)
[HTML]
http://wulrich.com/bimonthly_july2017.html (Part 2/2)
[PDF]
http://wulrich.com/downloads/bimonthly_may2017.pdf (Parts 1 and 2)

 

 

Introduction  To "understand" means to be able to formulate a question that is answered accurately by what one assumes that one knows, or which at least tells us accurately what we do not know.1) Hence if we want to understand what it means to be "competent" in systemic research practice, we need first of all to ask what sort of question we are trying to answer through such competence. As research students pursuing a Ph.D. or a Master of Science degree here in Lincoln, most of you are, among other things, interested in systems thinking. You believe (or perhaps merely hope) that systems thinking is a meaningful thing to study. You invest personal hopes, time and effort in order to qualify as a systems researcher. So, if systems thinking is (part of) the answer, what is the question?

Systemic thinking and research competence  I think it is indeed important for you to ask yourself this question. The way you understand "systemic" thinking will shape your understanding of "competent" research, and vice versa. For instance, it seems a reasonable starting point to assume that systemic thinking is about considering "the whole relevant system" that matters for understanding a problem or improving a situation. You will thus need to make sure that your problem definitions are large enough to include everything relevant; but what does that mean? Since we live in a world of ever-growing complexity, it could basically mean you need to do justice to the interdependencies of any problem with other problems, or of whatever aspects of the problem you focus on with other aspects of the same problem. So systemic thinking becomes the "art of interconnected thinking" (Vester (2007; cf. Ulrich, 2015), and you need to study methods for supporting such thinking. But then, making your problems large enough could also mean first of all to include a larger time horizon than usual, so as to make sure that problem solutions are sustainable over time; you would thus want to put the main focus of systemic thinking on ideas of sustainable development, on ecological and perhaps also evolutionary thought, and would have to acquire conforming knowledge and methods of inquiry. With equal right you might want to say that making problems large enough demands first of all that one consider the divergent views and interests of different parties concerned; which would associate systems thinking with multiple perspectives thinking, stakeholder analysis, participatory research approaches, and so on. As this short and very incomplete enumeration makes immediately clear, a "systemic" perspective lends itself to many different notions of what competent inquiry and practice can and should mean.

Accordingly important it is for you to as a research student to ask yourself what kind of competence you are striving for. The primary concern is competence, not systems thinking. How can you study successfully without a clear understanding of your goal? Of course your immediate goal is to get a degree; but I suppose getting a degree makes sense only if it is linked to personal learning and growth. By acquiring some of the specific skills that you expect from systems thinking, you may wish to deepen your competencies as a future professional or become a better researcher than you already are. Or you feel a need to strengthen your capabilities in general rather than just as a researcher. Perhaps you already feel confident about your professional training and experience but would like to become a more reflective professional or even a more mature person in general. You may then want to read this essay thinking of yourself as a "student of competence" rather than as a "student of systems thinking" and/or a "student of research"; for students of competence, I take it, we all remain throughout our lives.

Towards a personal notion of competence  Whatever your individual motives and state of preparation may be, I cannot formulate "the" relevant question for you. All I can attempt is to help you find your own individual question, by offering a few possible topics for reflection. As far as the paper also offers some considerations as to how you might deal with these topics, please bear in mind that I do not mean to claim these considerations are the only relevant or valid ones (a claim that again would presume one has found the one, right question to be asked when it comes to competence). I offer them as examples only. Their choice looks relevant to me at this particular moment in my academic and personal biography; but you are different persons and will therefore have to pursue your quest for competence in your own unique way. Contrary to academic custom, the game for once is not to be right but only to be true to yourself.

The Burden of Becoming a "Researcher"  As a research student you are supposed to do "research." Through your dissertation, you have to prove that you are prepared to treat an agreed-upon topic in a scholarly manner; in other words, that you are a competent researcher. Not surprisingly, then, you are eager to learn how to be a competent researcher. But I suspect that few of you are quite sure what precisely is expected from you. Hence the job of "becoming a competent researcher" is likely to sound like a tall order to you, one that makes you feel a bit uncomfortable, to say the least. What do you have to do to establish yourself as a "competent" researcher?

From what you have been told by your professors, you probably have gathered that being a competent researcher has something to do with being able to choose and apply methods. Methods, you have understood, should be appropriate to the problem you are dealing with and should help you to produce findings and conclusions that you can explain and justify in methodological terms. That is to say, you should be able to demonstrate how your findings and conclusions result from the application of chosen methods and why methods and results are all valid.

Questions concerning method  Previous to this seminar, I have spoken to many of you individually and I have felt that most of you worry a lot about which methods you should apply and how to justify your choices. It really seems to be an issue of choice rather than theory. There are so many different methods! The choice appears to some extent arbitrary. What does it mean to be a competent researcher in view of this apparent arbitrariness? You may have turned to the epistemological literature in order to find help, but what you have found is likely to have confused you even more. The prescriptions given there certainly seem abstract and remote from practice, apart from the fact that the diverse prescriptions often enough appear to conflict with one other.

As a second difficulty, once you have chosen a methodology and start to apply it, you will at times feel a strong sense of uncertainty as to how to apply it correctly. Methods are supposed to give you guidance in advancing step by step. You expect them to give you some security as to whether you are approaching your research task in an adequate way, so as to find interesting and valid answers to your research questions. But instead, what you experience is a lot of problems and doubts. There seem to be more questions than answers, and whenever you dare to formulate an answer, there again seems to be a surprising degree of choice and arbitrariness. What answers you formulate seems to be as much a matter of choice as what method you use and how exactly you use it.

Given this burden of personal choice and interpretation, you may wonder how you are supposed to know whether your observations and conjectures are the right ones. How can you develop confidence in their quality? How can you ever make a compelling argument concerning their validity? And if you hope that in time, as you gradually learn to master your chosen method, you will also learn how to judge the quality of your observations, as well as to justify the validity of your conclusions, yet a third intimidating issue may surface: how can you ever carry the burden of responsibility concerning the actual consequences that your research might have if it is taken seriously by other people, for example, in an organization whose problems you study and which then, based on your findings and conclusions, may implement changes that cost jobs or affects people in other ways?

As a fourth and final example of such worries, your major problem may well be to define "the problem" of your research, that is, the issue to which you are supposed to apply methods in a competent fashion. This is indeed a crucial issue, but here again the epistemological and the methodological literature is rarely of help. Its prescriptions seem so remote from your needs!

A lot of questions to worry about, indeed. But didn't we just say that without questions there is no understanding? So take your questions and doubts as a good sign that you are on your way towards understanding. Let us explore together where this way might lead you. One thing seems certain: if you do not try to understand where you want to go, you are not likely to arrive there!

The Death of the Expert2)  Sometimes it is easier to say what our goal is not, rather than what it is. Are there aspects or implications of "competence" that you might wish to exclude from your understanding of competence in research? Certainly.

For instance, in what way do you aim to be an "expert" on systems methodologies (or any other set of methodologies), and in what way do you not want to become an "expert"? To be competent in some field of knowledge means to be an expert, doesn't it? The role that experts play in our society is so prominent and seemingly ever more important that a lot of associations immediately come to our mind. To mention just three: experts seem to be able to make common cause with almost any purpose; most of the time (except when they are talking about something we, too, happen to be experts in) experts put us in the situation of being "lay people" or non-experts (i.e., incompetent?); experts frequently cease to reflect on what they are doing and claiming. So, are there roles you would rather not want to play, causes you'd rather not serve, as a competent researcher? Are there circumstances or situations in which you would rather not claim to be an expert, that is, rely on, and refer to, your "expertise"? Where do you see particular dangers of ceasing to be self-critical?

Expertise or the pitfall of claiming too much Ceasing to be self-critical, with the consequent risk of claiming too much, is unfortunately very easy. There are so many aspects of expertise or competence that need to be handled self-critically! So much seems clear: as competent researchers we do not want to ignore or conceal the limitations of the methods on which our competence depends – "methods" in the widest possible sense of any systematically considered way to proceed. The limitations of a method are among its most important characteristics; for if we are not competent in respecting these limitations, we are not using the method in a competent manner at all. Hence, one of the first questions we should ask about every method concerns its limitations.

Technically speaking, the limitations of a method may be said to be contained in the theoretical and methodological assumptions that underpin any reliance on it. Some of these may be built into a method we use; others may arise due to the imperfect ways in which we use it, for example, if we don't master the method or use it in biased ways.

Perhaps an even more basic assumption is that experts, by virtue of their expertise, have a proper grasp of the situations to which they apply their expertise, so that they can properly judge what method is appropriate and this choice will then ensure valid findings and conclusions. Experts often seem to take such assumptions for granted, or else tend to cover them behind a facade of busy routine.

Sources of deception  To the extent that we are insensible to these assumptions, they threaten to become sources of deception. We ourselves may be deceived as researchers, but inadvertently we may also deceive those who invest their confidence in our competence. There need not be any deliberate intention to deceive others on the part of the researcher; it may simply be routine that stops researchers from revealing to themselves and to others concerned the specific assumptions that flow into every concrete application of their expertise. Even so, this is probably not what you would like to understand by "competence."

The earlier-mentioned questions and doubts that plague many a research student are then perhaps indeed a healthy symptom that your research competencies have not yet reached the stage of routine where such lack of reflection threatens. This danger is more of a threat to established researchers who have already become recognized as experts in their field of competence. Although some degree of routine is certainly desirable, it should not be confused with competence. Routine implies economy, not competence.

When experts forget this distinction, they risk suffering the silent death of the expert. It seems to me at times that in our contemporary society, the death of the expert has taken on epidemic dimensions! We are facing an illness that has remained largely unrecognized or incorrectly diagnosed, perhaps because it causes an almost invisible death, one that often enough is hidden by the vigorous and impressive behavior patterns of those who have developed the disease.

There is a second cause of the death of the expert that we must consider. Even if a researcher remains thoroughly aware of the methodological and theoretical underpinnings of his or her competence and makes an appropriate effort to make them explicit, does that mean that the research findings provide a valid ground for practical conclusions? This is often assumed to be the case, but repeated assumption does not make a proposition valid. A sound theoretical and methodological grounding of research – at least in the usual understanding of "theory" and "methodology" – implies at best the empirical (i.e., descriptive) but not the normative (i.e., prescriptive) validity of the findings. Well-grounded research may tell us what we can and cannot do, but this is different from what we should do on normative grounds.

The virtue of self-limitation  When it comes to that sort of issue, the researcher has no advantage over other people. Competence in research then gains another meaning, namely, that of the researcher's self-restraint. No method, no skill, no kind of expertise answers all the questions that its application raises. One of the most important aspects of one's research competence is therefore to understand the questions that it does not answer.

The number of questions that may be asked is, of course, infinite – as is, consequently, the number of questions that competence cannot be expected to answer. You have thus good reason to worry about the meaning of competence in research. If you want to become a competent researcher, you should indeed never stop worrying about the limitations of your competence! As soon as you stop worrying, the deadly disease may strike. The goal of your quest for competence is not to be free of worries but rather to learn to make them a source of continuous learning and self-correction. That is the spirit of competent research. Competence in research does not mean that research becomes a royal road to certainty. What we learn today may (and should) always make us understand that what we believed yesterday was an error. The more competent we become as researchers, the more we begin to understand that competence depends more on the questions we ask than on the answers we find. It is better to ask the right questions without having the answers than to have the answers without asking the right questions. If we do not question our answers properly, we do not understand them properly, that is, they do not mean a lot.

This holds true as much in the world of practice as in research, of course. The difference may be that under the pressures of decision making and action in the real world, the process of questioning is often severely constrained. It usually stops as soon as answers are found that serve the given purpose. As a competent researcher, your focus will be more on the limitations of the answers and less on limiting the questions. This is what a researcher's well-understood self-limitation is all about.

A preliminary definition of competence in research  Your tentative first definition of competency in research, then, might be something like this (modify as necessary):

Competence in research means to me pursuing a self-reflective, self-correcting, and self-limiting approach to inquiry. That is, I will seek to question my inquiry in respect of all conceivable sources of deception, for example, its (my) presuppositions, its (my) methods and procedures, and its (my) findings and the way I translate them into practical recommendations.

In this tentative definition, the pronoun "its" refers to the inherent limitations of whatever approach to inquiry I may choose in a specific situation, limitations that are inevitable even if I understand and apply that approach in the most competent way. The pronoun "my," in contrast, refers to my personal limitations in understanding and applying the chosen approach. Accordingly, the essential underlying question is how as a researcher you are to deal adequately with these limiting factors in the quest for relevant, valid, and responsible research. The three underlined phrases stand for key notions in my personal attempt to respond to this question. Given their personal nature, I encourage you to interpret, question and modify them according to your own experiences, needs, and hopes. Do not allow your thinking to be limited by them! The only reason I introduce them here is that they inform my personal concept of research and thus may help you in better understanding (and thus questioning) the reflections on the nature of competent research offered in this essay.

A major implication of this preliminary definition is the following. Competence in research means more – much more – than mastering some research tools in the sense of knowing what methodology to choose for a certain research purpose and how to apply it in the specific situation of interest. Technical mastery, although necessary, is not equal to competence. It becomes competence only if it goes hand in hand with at least two additional requirements:

(a) that we learn to cultivate a continuous (self-) critical observation of the built-in limitations of a chosen research approach – "observing" its limitations, that is, in the double sense of "understanding" and "respecting" them; and, perhaps even more importantly and certainly more radically,

(b) that we quite generally renounce the notion that we can ever justify the validity of our eventual findings by referring to the proper choice and application of methods.

The obvious reason for (b) is that justifying findings by virtue of methods does little to justify the selectivity of those findings regarding both their empirical and their normative content, that is, the circumstances taken to be relevant for understanding a situation and the criteria considered adequate for evaluating or improving it. Selectivity results from inherent limitations of methods as well as from the limitations of our resources and understanding in applying them (which is not to say that there are no other sources of selectivity, such as personal world views and interests or institutional, political and economic mechanisms and pressures).

The limited justificatory power of methods is bad news, I fear, for some of you who probably have been taught to base your search for competence on the idea of a theoretically based choice among methodologies. To be sure, there is nothing wrong with this idea – so long as you do not expect it to ensure critical inquiry. The notion of securing critical inquiry and practice through theoretically based methodology choice is currently prominent in systems research and particularly in the methodological discussions around the notion of critical systems thinking (CST); but I invite you to adopt it with caution. It does not carry far enough.3)

Further sources of orientation and questioning  We must ask, then, what else can give us the necessary sense of orientation and competence in designing and critically assessing our research, if not (or not alone) the power of well-chosen methods? I suggest that you consider first of all the following three additional sources of orientation that I have found valuable (among others), namely:

• understanding your personal quest for "improvement" in each specific inquiry;

• observing what following Kant I call "the primacy of practice in research";

• recognizing and using the significance of C.S. Peirce's "pragmatic maxim."

Further considerations will then concern the concepts of

• "systematic boundary critique";

• "high-quality observations";

• cogent reasoning or compelling argumentation;

• mediating between theory and practice (or science and politics); and finally,

• the "critical turn" that informs my work on critical systems heuristics.

The Quest for Improvement  One of the sources of orientation that I find most fundamental for myself is continuously to question my research with regard to its underlying concept of improvement. How can I develop a clear notion of what, in a certain situation, constitutes "competent" research, without a clear idea of the difference it should make?

The "difference it should make" is a pragmatic rather than merely a semantic category, that is, it refers to the implications of my research for some domain of practice. If I am pursuing a purely theoretical or methodological research purpose, or even meta-level research in the sense of "research on research," the practice of research itself may be the domain of practice in which I am interested primarily; but when we do "applied" research in the sense of inquiry into some real-world issue, it will have implications for the world of social practice, that is, the life-worlds of individuals and their interactions in the pursuit of individual or collective (organizational, political, altruistic, etc.) goals.

In either case I will need to gain a clear idea of the specific domain of practice that is to be improved, as well as of the kind of improvement that is required. One way to clarify this issue is by asking what group of people or organizations belong to the intended "client" (beneficiary) of a research project, and what other people or organizations might be affected, whether in a desired or undesired way. (Note that from a critical point of view, we must not lightly rule out the possibility of undesired side-effects; hence, when we seek to identify the people or organizations that might be affected, we should err on the side of caution and include all those whom we cannot safely assume not to be affected.) Together these groups of people or organizations constitute the domain of practice that I will consider as relevant for understanding the meaning of "improvement."

What makes research valuable? Once the client and the respective domain of practice are clear, the next question concerns the sort of practice that my research is supposed (or, critically speaking, likely) to promote. The competence of a research expresses itself not by its sheer beauty but by its value to the practice it is to support. In order to have such value, it must be relevant – answer the right questions; and valid – give the right answers. But how can we, as researchers, claim to know (i.e., stipulate) the kind of practice to which we should contribute? Have we not been taught long enough that competent ("scientific") inquiry should refrain from being purpose and value driven?

The German sociologist and philosopher of social science Max Weber (1991, p. 145) has given this concern its most famous formulation: "Politics is out of place in the lecture room." I can appreciate Weber's critical intent, namely, that academic teaching should be oriented towards theory rather than towards ideology. But can that mean, as Weber is frequently understood, that research is to be "value-free"?4) A better conclusion, in my opinion, would be that as researchers we must make it clear to ourselves, and to all those concerned, what values our research is to promote and whose values they are; for whether we want it or not, we will hardly ever be able to claim that our research serves all interests equally. We cannot gain clarity about the "value" (relevance and validity) of our research unless we develop a clear notion of what kind of difference it is going to make and to whom. A clear sense of purpose is vital in competent research.

If you have experienced blockages in advancing your project, for example in defining research strategies and so on, ask yourself whether this might have to do with the lack of a sense of purpose. When you do not know what you want to achieve, it is very difficult indeed to develop ideas. Conversely, when your motivation and your vision of what you want to achieve are clear, ideas will not remain absent for long. Your personal vision of the difference that your research should make can drive the process of thinking about your research more effectively than any other kind of reflection.

The Primacy of Practice  As research students studying for a Ph.D. or M.Sc. degree, your preoccupation with the question of "how" to do proper research is sound. But as we have just seen, the danger is that as long as you put this concern above all others, it will remain difficult to be clear about what it is that you want to achieve. For it means that you rely unquestioningly on a very questionable assumption, namely, that good practice (P) – "practice" in the philosophical sense of praxis rather than in the everyday sense of "exercise" – is a function (f) of proper research (R), whereby "proper" essentially refers to adequate research methodology:

P = f (R)

Good research should of course serve the purpose of assuring good practice; but does it follow that the choice of research approaches and methods should determine what is good practice? I do not think so. Quite the contrary, it seems to me that good research should be a function of the practice to be achieved:

R = f (P)

Your primary concern, then, should not be how to do proper research but what for. This conjecture requires an immediate qualification, though, concerning the source of legitimation for the "what for." Note that in our inverted formula, practice (P) is no longer the dependent variable but is now the independent variable. This is precisely as it should be: It is not up to the researcher to determine what is the right (legitimate) "what for." Rather, it is the researcher's obligation to make it clear to herself or himself, and to all those concerned, what might be the practical implications of the research, that is, what kind of practice it is likely to promote –the factual "what for."

After that, practice must itself be responsible for its purposes and measures of improvement. Researchers may be able to point out ways to "improve" practice according to certain criteria, but they cannot delegate to themselves the political act of legitimizing these criteria (cf. Ulrich, 1983, p. 308). It is an error to believe that good practice can be justified by reference to the methods employed. Methods need to be justified by reference to their implications for practice, not the other way round!

In competent research, the choice of research methods and standards is secondary, that is, a function of the practice to be achieved. Good practice cannot be justified by referring to research competence. Hence, let your concern for good research follow your concern for understanding the meaning of good practice, rather than vice versa.

The suggested primacy of the concern for the outcome of a research project over the usually prevailing concern for research methodology (the "input," as it were) is somewhat analogous to the primacy that Kant assigns to the practical over the theoretical (or speculative) employment of reason, or to what he refers to as the "primacy of practical reason in its union with speculative reason" (Kant, 1788, A 215, 218; cf. 1787, B 824f, 835f). Theoretical reason can generate valid knowledge only within the bounds of experience; but practical reason can conceive of ideas such as the moral idea that help us ensure good practice and thereby to create a new, different reality. Theoretical reason can tell us what we can and can't do and how to achieve it, but not what for (to what ends and according to what standards) we should try to achieve it. For Kant it is therefore practical-moral rather than theoretical-instrumental reasoning that has to play a leading role in the way we use reason, for it alone can lead us beyond the latter's limitations. I would therefore like to think of our conclusion in terms of a primacy of practice in research. But again, the point is not that it is upon the researcher to determine the right "what for"; the point is, rather, that well-understood reasoning involves a normative dimension for which theoretical and methodological expertise does not provide a privileged qualification.

Towards a two-dimensional concept of research competence  Accordingly, the concept of competent research that I suggest here is based on Kant's two-dimensional concept of reason. This distinguishes it from the more usual concept of competence in research and professional practice that is implicit in most contemporary conceptions of knowledge and of science and which has lost sight of the normative dimension of rationality. I am thinking particularly of the model of empirical-analytic science (so-called science-theory) that has come to dominate the actual practice of science in many domains, a model that is rooted in the logical empiricism of the so-called Vienna Circle of the 1930s (Schlick, Carnap, Reichenbach and others) but which has since been developed and has found its most widely adopted expression today in the work of Popper (1959, 1963, 1972) on "critical rationalism." Symptomatically, Popper replaced Kant's primacy of practical over theoretical reason with a one-sided primacy of theory, a model that in effect reduces practical to instrumental reason while relegating practical reasoning properly speaking, including moral reasoning, to a merely subjective and indeed non-rational status. For those interested, I have elsewhere explained and discussed this prevalent but impoverished model of rationality, for which the reach of reason is equal to that of science, in detail (see, e.g., Ulrich, 1983 and 2006c).

To conclude this brief discussion of the suggested primacy of practice in research, let us consider an example of what it means in actual research practice. Research into poverty provides a good illustration with which I am familiar through my own engagement in this field (Ulrich and Binder, 1998). Poverty researchers are often expected to tell politicians "objectively" how much poverty there is in a certain population and what can be done about it. But measuring poverty is not possible unless there are clear criteria of what standards of income, well-being, and participation in society (both material and immaterial) are to be considered "normal" for a decent life and accordingly should be available to all members of that population. If poverty research is to be done in a competent way, so that it can tell us who and how many of us are poor and what are their needs, there must first be a concrete vision of the kind of just society to be achieved! This is what I mean by the primacy of practice in research.

The Pragmatic Maxim  The orientation provided by a well-understood primacy of practice must not be confused with mere "pragmatism" in the everyday sense of orientation toward what "works" or serves a given purpose. The point is not utilitarianism but the clarity of our thinking that we can obtain through clarity of purpose. This idea was first formulated by Charles S. Peirce (1878) in his pragmatic maxim, in a now famous paper with the significant title "How to make our ideas clear":

Consider what effects, which might conceivably have practical bearings, we conceive the object of our conception to have. Then, our conception of these effects is the whole of our conception of the object. (Peirce, 1878, para. 402)

The pragmatic maxim requires from us a comprehensive effort to bring to the surface and question the implications (i.e., the actual or potential consequences) that our research may have for the domain of practice under study. Contrary to popular pragmatism, according to which "the true is what is useful," the pragmatic maxim for me represents a critical concept. The true is not just what is useful but what considers all practical implications of a proposition, whether it supports or runs counter to my purpose. Uncovering these implications thus becomes an important virtue of competent inquiry and design in general, and of critical systems thinking in particular.

Pragmatism calls for a critical stance  There is a crucial critical kernel in the pragmatic maxim that we need to uncover and move to the center of our understanding of pragmatism. I understand it as follows. Identifying the actual or conceivable consequences of a proposition, as Peirce requires it of a pragmatic researcher, is not a straightforward task of observation and reasoning but raises difficult theoretical as well as normative issues. Theoretically speaking, the question is, what can be the empirical scope of our research? Normatively speaking, the question is, what should we consider as relevant practical implications? Peirce's solution is of course to consider all conceivable implications; but for practical research purposes that answer begs the question. The question is, how can we limit the inquiry to a manageable scope yet claim that its findings and conclusions are relevant and valid? The quest for comprehensiveness is reserved to heroes and gods; it is beyond the reach of ordinary researchers. What we ordinary researchers recognize as relevant implications depends on boundary judgments by which we consciously or unconsciously delimit the situation of concern, that is, the totality of "facts" (empirical circumstances) and "norms" (value considerations) that determine the definition of "the problem" and its conceivable "solutions." The response to Peirce's challenge can thus only be that we must make it clear to ourselves, and to all others concerned, in what way we (or they) may fail to be comprehensive, by undertaking a systematic critical effort to disclose those boundary judgments.

Systematic Boundary Critique  In Critical Heuristics (Ulrich, 1983, see esp. Chapter 5), I conceived of this critical effort as a process of systematic boundary critique,5) that is, a methodical process of reviewing boundary judgments so that their selectivity and changeability become visible. Table 1 shows a list of boundary questions that can be used for reviewing a claim's sources of selectivity; you’ll find elsewhere more complete accounts of the boundary categories that inform these questions, and of the underlying framework of critical systems heuristics (CSH).6)

Table 1: Sources of selectivity:
The boundary questions of critical systems heuristics

(Adapted from Ulrich, 1984, p. 338-340; 1987, p. 279; 1993, p. 597;
1996a, pp. 24-31; 2000, p. 258)

SOURCES OF MOTIVATION

(1)  Who is (ought to be) the client? That is, whose interests are (should be) served?

(2)  What is (ought to be) the purpose? That is, what are (should be) the consequences?

(3)  What is (ought to be) the measure of improvement? That is, how can (should) we determine whether and in what way the consequences, taken together, constitute an improvement?

SOURCES OF POWER

(4)  Who is (ought to be) the decision maker? That is, who is (should be) in a position to change the measure of improvement?

(5)  What resources are (ought to be) controlled by the decision maker? That is, what conditions of success can (should) those involved control?

(6)  What conditions are (ought to be) part of the decision-environment? That is, what conditions does (should) the decision maker not control (e.g., from the viewpoint of those not involved)?

SOURCES OF KNOWLEDGE

(7)  Who is (ought to be) involved as a professional? That is, who is (should be) involved as an expert, e.g., as a system designer, researcher, or consultant?

(8)  What expertise is (ought to be) consulted? That is, what counts (should count) as relevant knowledge?

(9)  What or who is (ought to be) assumed to be the guarantor? That is, what is (should) be considered a source of guarantee (e.g., consensus among experts, stakeholder involvement, support of decision-makers, etc.)?

SOURCES OF LEGITIMATION

(10)  Who is (ought to be) witness to the interests of those affected but not involved? That is, who is (should be) treated as legitimate stakeholder, and who argues (should argue) the case of those stakeholders who cannot speak for themselves, including the handicapped, the unborn, and non-human nature?

(11)  What secures (ought to secure) the emancipation of those affected from the premises and promises of those involved? That is, where does (should) legitimacy lie?

(12)  What world view is (ought to be) assumed? That is, what different visions of improvement are (should be) considered and somehow reconciled?

For me this critical effort of disclosing and questioning boundary judgments serves a purpose that is relevant both ethically and theoretically. It is relevant theoretically because it compels us to consider new "facts" that we might not consider otherwise; it is relevant ethically because these new facts are likely to affect not only our previous notion of what is empirically true but also our view of what is morally legitimate, that is, our "values."

To be sure, what I propose to you here is not as yet a widely shared concept of competence in research, but I find it a powerful concept indeed. Once we have recognized the critical significance of the concept of boundary judgments, we cannot go back to our earlier, "pre-critical" concept of competent research in terms of empirical science only. It becomes quite impossible to cling to a notion of competent research that works in just one dimension. This is so because what we recognize as "facts" and what we recognize as "values" become interdependent.

The question of what counts as knowledge, then, is no longer one of the quality of empirical observations and underpinning theoretical assumptions only; it is now also a question of the proper bounding of the domain of observation and thus of the underpinning value judgments as to what ought to be considered the relevant situation of concern. What counts as knowledge is, then, always a question of what ought to count as knowledge. We can no longer ignore the practical-normative dimension of research or relegate it to a non-rational status.

 End of Part 1/2, continued with Part 2/2 >>

 

 

 

Notes

1) The British philosopher, historian, and archaeologist R.G. Collingwood (1939/1983, 1946) was perhaps the first author to systematically discuss the logic of question and answer as a way to understand the meaning of everyday or scientific propositions. As he explains in his Autobiography (1939):

I began by observing that you cannot find out what a man means by studying his spoken or written statements, even though he has spoken or written with perfect command of language and perfectly truthful intention. In order to find out his meaning you must also know what the question was (a question in his mind, and presumed by him to be in yours) to which the thing he has said or written was meant as an answer.
   It must be understood that question and answer, as I conceived them, are strictly correlative.… [But then,] if you cannot tell what a proposition means unless you know what question it is meant to answer, you will mistake its meaning if you make a mistake about that question.… [And further,] If the meaning of a proposition is correlative to the question it answers, its truth must be relative to the same thing. Meaning, agreement and contradiction, truth and falsehood, none of these belonged to propositions in their own right, propositions by themselves; they belonged only to propositions as the answers to questions. (Collingwood, 1939/1978, pp. 31 and 33, italics added) 

While remaining rather neglected in fields such as science theory and propositional logic, it was in the philosophy of history (the main focus of Collingwood, esp. 1946), along with hermeneutics (Gadamer, 2004), and argumentation theory (Toulmin, 1978, 2003) that Collingwood's notion of the logic of question and answer was to become influential. In hermeneutic terms, the questions asked are an essential part of the hermeneutical horizon that shapes what we see as possible answers and what meaning and validity we ascribe to them. In his seminal work on hermeneutics, Truth and Method, Gadamer (2004) notes:

Interpretation always involves a relation to the question that is asked of the interpreter.… To understand a text means to understand this question.… We understand the sense of the text only by acquiring the horizon of the question – a horizon that, as such, necessarily includes other possible answers. Thus the meaning of a sentence … necessarily exceeds what is said in it. As these considerations show, then, the logic of the human sciences is a logic of the question.
   Despite Plato we are not very ready for such a logic. Almost the only person I find a link with here is R.G. Collingwood. In a brilliant and telling critique of the Oxford "realist" school, he developed the idea of a logic of question and answer, but unfortunately never elaborated it systematically. He clearly saw that … we can understand a text only when we have understood the question to which it is an answer. (Gadamer, 2004, p. 363)  [BACK]

2) As I found out after writing the original working paper (Ulrich, 1998a), the phrase "death of the expert" is not mine. White and Taket (1994) had used it before. By the time I prepared the expanded version of the essay for Systems Research and Behavioral Science (Ulrich, 2001a), I had become aware of their earlier use of the phrase and accordingly gave a reference to it. My discussion here remains independent of theirs, but I recommend readers to consult their different considerations as well.  [BACK]

3) We'll return to this issue under the heading of "methodological pluralism" below. For a systematic account and critique of the identification of critical practice with methodology choice in this strand of critical systems thinking (CST), see Ulrich (2003) and the ensuing discussions in several subsequent "Viewpoint" sections of the journal. Readers not familiar with CST may find Ulrich (2012e or 2013b) useful preparatory reading.  [BACK]

4) I have given an extensive critical account of Weber's notion of "value-free" interpretive social science and his underlying conception of rationality elsewhere, see Ulrich (2012b). We will return to Weber's "interpretive social science" in the section on theory and practice below.  [BACK]

5) I use the term "boundary critique" as a convenient short label for the underlying, more accurate concept of a "critical employment of boundary judgments." The latter is more accurate in that it explicitly covers two very different yet complementary forms of "dealing critically with boundary judgments." It can be read as intending both a self-reflective handling of boundary judgments (being critical of one's own boundary assumptions) and the use of boundary judgments for critical purposes against arguments that do not lay open the boundary judgments that inform them (arguing critically against hidden or dogmatically imposed boundary assumptions). By contrast, the term "boundary critique" suggests active criticism of other positions and thus, as I originally feared, might be understood only or mainly or only in the second sense. While this second sense is very important to me, the first sense is methodologically more basic and must not be lost. I would thus like to make it very clear that I always intend both meanings, regardless of whether I use the original full concept or the later short term.

Terms do not matter so much and represent no academic achievement by themselves, only the concepts or ideas for which they stand do and these should accordingly be clear. The concept of a critical employment of boundary judgments in its mentioned, double meaning embodies the methodological core principle of my work on critical systems heuristics (CSH) and accordingly can be found in all my writings on CSH from the outset (e.g., Ulrich, 1983, 1984, 1987, 1988, 1993, etc.). Only later, beginning in 1995, I have introduced the short label "boundary critique" (see, e.g., Ulrich, 1995, pp. 13, 16-18, 21; 1996a, pp. 46, 50, 52; 1996b, pp. 171, 173, 175f; 1998b, p. 7; 2000, pp. 254-266; and 2001, pp. 8, 12, 14f, 18-20, 24). Meanwhile I have increasingly come to find it a very convenient label indeed, so long as it is clear that both meanings are meant (and in this sense I use it as a rule). Accordingly I am now employing it regularly and systematically (cf., e.g., Ulrich, 2002, 2003, 2005, 2006a, 2012 b, c, d; 2013b; and most recently, 2017).  [BACK]

6) The boundary questions presented here are formulated so that the second part of each question defines the boundary category at issue. For introductions of varying depth and detail to the boundary categories and questions of CSH, see, e.g., Ulrich, 1983, esp. pp. 240-264; 1984, pp. 333-344; 1987, p. 279f; 1993, pp. 594-599; 1996a, pp. 19-31, 43f; 2000, pp. 250-264; 2001a, pp. 250-264; and 2001b, pp. 91-102. On CSH in general, as well as the way it informs my two research programs on "critical systems thinking (CST) for citizens" and on "critical pragmatism," also consult: Ulrich 1988, 2000, 2003, 2006a, b, 2007a, b, 2012b, c, d, 2013b, and 2017, and Ulrich and Reynolds, 2010.  [BACK]

 

 

 

May 2017

Su
Mo
Tu
We
Th
Fr
Sa
 
1
2
 3
 4
 5
 6
 7
 8
 9
10
11
12
13
14
15
16
17
18
19
20
21
22
23
24
25
26
27
28
29
30
31
 
 
 
 
 
 
 
 
 
 

June 2017

Su
Mo
Tu
We
Th
Fr
Sa
 
 
 
  
1
 2
 3
 4
 5
 6
 7
 8
9
10
11
12
13
14
15
16
17
18
19
20
21
22
23
24
25
26
27
28
29
30
 
 
 
 
 
 
 
 
   

 

 

 

 

References

Please see the cumulated references at the end of Part 2.
The following link leads you directly there (in a new frame or tab).

 Cumulated references at the end of Part 2/2 >>

Subsequently, in the new frame (or tab) that has opened with the References, hit the Back button of your browser to return to the present place and close the additional frame. (Note: this may not work on all devices. In this case, you can still use the ordinary "Previous" buttons that you find at the top and the bottom of every Bimonthly page.

 

Picture data  Digital photograph taken on 8 August 2010, around 4 p.m., in the author's garden. ISO 200, exposure mode aperture priority with aperture f/7.1 and exposure time 1/25 seconds, exposure bias -0.70. Metering mode center-weighted average, contrast soft, saturation high, sharpness low. Focal length 102 mm (equivalent to 204 mm with a conventional 35 mm camera). Original resolution 3648 x 2736 pixels; current resolution 700 x 525 pixels, compressed to 236 KB.

May-June, 2017

Competent practice involves boundary critique

 Competent practice involves a proper handling of boundary judgments 

Once we have recognized the critical significance of boundary judgments, we cannot go back to our earlier, pre-critical concept of competent research.”

(From this essay on the nature of systemic research and practice)

Notepad for capturing personal thoughts  »

Previous Picture

Next Picture  

Personal notes:

Write down your thoughts before you forget them!
Just be sure to copy them elsewhere before leaving this page.

 

 

 

 

 

 

Last updated 10 Sep 2017 (first published 28 Aug 2017)
http://wulrich.com/bimonthly_may2017.html

 

 

  

 

 

 

 

 

 

 

 

 .