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On Relevance

The Walter and Eliza Hall Institute of Medical Research, Victoria, Australia

Key Words. Relevance • Manuscript citation • Research techniques

Dr. Donald Metcalf, The Walter and Eliza Hall Institute of Medical Research, Post Office 3050, Royal Melbourne Hospital, Victoria, Australia.

As a compulsive worker, unable to undertake purportedly health-giving regular physical exercise, I had not really envisaged reaching 70 and finding myself still working a full day at the bench. When the then-legal age for retirement at 65 approached for me, it was clear enough that I should vacate my existing position in the Institute and thereafter keep a low profile. So much was common courtesy toward my younger colleagues, ready and willing to chance their arm. What was equally apparent, however, was that because I had many experiments in progress, it made no sense to cease this activity. Indeed, because I usually work on team projects initiated with my colleagues, my scientific life presumably could continue very much as it had previously, with its daily data gathering, interspersed with the usual kaleidoscopic patches of frustration or excitement.

These readjustments have in fact occurred and, if my position on the authors' list is now often lower than it once was, there remain regular first-author manuscripts and nothing much appears to have changed in daily laboratory life.

Change there has been, however, and change that I had not envisaged. My situation as an active but elderly research worker is rather uncommon and there were few examples among my contemporaries or predecessors to alert me to what was likely to happen. Although it happened slowly, and in the nicest possible way, I perceived myself becoming increasingly irrelevant to my colleagues in the field.

This perception may, of course, have been a mistaken impression due to my somewhat hypersensitive state. Furthermore, relevance is a somewhat intangible quality, easily confused with influence; the latter often being the consequence of position or power.

After the first shock of realization that I was now beginning to be judged irrelevant, I have spent some time reflecting on the nature and origins of the state of relevance. Who or what defines relevance? Why does a judgment on relevance matter? How does one assess one's personal relevance or the relevance of one's current research? Can one minimize or avoid the risk of becoming irrelevant?

	Parameters for Assessing Personal Relevance

Top Parameters for Assessing... Assessment of the Perceived... Publications, Citations and... Methods for Sustaining Relevance Conclusions

 
In the best of all possible worlds, having made innovative and sustained contributions to knowledge in a particular field, one should thereafter remain in a state of relevant grace. Unfortunately, things do not work out like this in biological research for a variety of reasons.

As one's original contributions are expanded upon by others, properly enough, attention switches to the more prominent of these refiners and polishers. This seems to be a fate that is characteristic of scientists as distinct, for example, from that of painters or composers whose innovative works tend to remain cherished.

By today's somewhat dubious standards, mandatory reference in a scientific paper to the preceding work of others seems to have a narrow time window of around two years. Work performed in that period must be quoted and acknowledged: work performed before this period can apparently either be largely ignored or referred to via some convenient review. Furthermore, subfields of scientific discovery or inquiry fluctuate in their current popularity very much as do clothing fashions. The darlings of the moment and their subfield seem usually to enjoy a period of prominence for relatively short periods of 5 to 10 years before sinking into relative obscurity. This need not be a permanent state and the field may subsequently experience further waves of cutting-edge status, but the cycles are clearly evident.

The personal experience of most scientists is dictated by these general features of the natural history of biological research. Any attempted assessment of one's current personal level of acceptance or relevance needs therefore to take into account the cycle status of one's field.

As noted earlier, in attempting an assessment of personal relevance, one needs to be careful to distinguish relevance from either reputation (a parameter of past performance) or influence (a parameter that may simply indicate one's position-based ability to influence what one's colleagues do, if not think).

There are a number of simple parameters available for self-assessment of current personal relevance. Are you included in lunch-break scientific conversations between colleagues or visiting scientists? Are your seminars well attended? Do they arouse vigorous and critical discussion? How many requests for collaborative studies are you receiving? Are you receiving regular requests to write news and views sections for journals, mini-reviews or (the pinnacle) requests for reviews in Nature, Science, or Cell? In curious contrast, requests to referee manuscripts or grant applications seem to have no relation to one's current relevance rating.

There are also some revealing parameters for assessing personal relevance to be deduced from the structure of scientific meetings and what actually happens during such meetings. Individuals whose work is followed by colleagues with anticipation or trepidation clearly are being regarded as currently relevant. These are the investigators who will find themselves scheduled to speak in presidential symposia or in prime-time single-session symposia. The auditorium will be full on such occasions and the audience will be attentive. The signs are ominous if one finds oneself consistently being omitted from this list of stars of the moment, or if the auditorium empties on your arrival at the podium.

To become a consistent invitee to give an opening keynote address is also a potentially ominous sign, the more so if again the auditorium is only half full during the address. After all, how many delayed flights or buses are there? A keynote invitation may be intended as a recognition by one's colleagues of good past work and, as such, is a kindly act. Indeed, there are a fortunate few with an encyclopedic enough memory and sufficient grasp of the complexity of current literature to turn such performances into memorable occasions. However, with a part-empty auditorium, the message becomes very clear— the work and/or the speaker is being considered irrelevant. No matter how balanced the synthesis of information, no matter what flashes of insight and simplification are revealed, the audience is no longer hungering for the product.

Oddly enough, prize-winning and election to academies are not parameters of current relevance. Prizes and academic honors are awarded retrospectively and are occasions on which past work, often decades previously, is given prominent and balanced assessment.

Application of these parameters to assess my current personal relevance is providing a mixed answer. By some of these parameters, I am being considered irrelevant. Strangely, however, I am receiving increasing requests for collaborative studies. Is this a sign of relevance or am I simply being recognized as a reliable, super-technician? I suspect the latter, but as we shall see later, I do not accept that irrelevance is a wholly irreversible state and to be adept and perceptive experimentally is the potential key for re-entry into the state of being relevant.

The answer to the first question—relevant to whom?—is clearly therefore relevant to one's colleagues and competitors in one's own field of research and, possibly, to those in related biological fields.

An assessment of current personal relevance is not simply a matter of personal self-esteem. This is actually an important judgment made by others that can seriously affect one's ability to perform research. To explore the reasons why this is so, we need to consider the second question—relevant to what? Here the question relates to whether the particular projects in which one is engaged are considered by one's peers to be of relevance to the current state of the field. What is at issue here is not how well the experiments are being executed but whether they are judged as being of current relevance or importance.

	Assessment of the Perceived Relevance of Projects

Top Parameters for Assessing... Assessment of the Perceived... Publications, Citations and... Methods for Sustaining Relevance Conclusions

 
A general assessment of the relevance of the work in progress of an individual or a group requires certain preliminary criteria to be met. Are the methods being used still adequately state-of-the-art or have they become outmoded? Are the approaches employing a broad enough range of technology? Is the teamwork efficient and regularly productive? If so, then discoveries in the project will depend on hard work, astute observation, experience and, as always, a certain amount of luck. By these preliminary criteria, our present group can be regarded as an effective research team, but is their work accepted as being of current relevance or importance, either by the field or by the broader population of biological scientists?

There are certain defined goals which we in medical research collectively seek to attain. For example, in my field of cancer research, we presumably all hope to achieve the ultimate goals of identifying the causes of cancer and of developing practicable methods for preventing or greatly reducing the occurrence of cancer. Should these goals remain completely unattainable, we would hope to develop treatment methods that are clearly better than the now aging surgery-cytotoxic therapeutic approaches whose success is at best patchy. For cancer research workers, these goals determine the primary definition of relevance. Any work making progress in one or other of this complex of questions is clearly of relevance, if only for one type of cancer. Relevance here includes endpoints that are independent of one's current colleagues in the field but also includes judgments by those same colleagues on whether the work is of current relevance.

Problems arise when most workers come to the recognition that the major goals are indeed distant and, in terms of daily work, a little unrealistic. We come to accept the reality that our own particular contributions are at best going to be stepping stones somewhere along the way to the major goals and we progressively design our experiments to be less grandiose, more attainable and often, arguably, not directly related to the big goals. It is now that major differences can arise in group judgments as to what is important or front-running in respect of these restricted goals.

The situation becomes more complex if the view is taken that a proper understanding of the function of normal cells and tissues may be essential to achieve an adequate understanding of the nature of the corresponding cancer cells. While most would accept this as an intellectual proposition, in practice a very clear division becomes evident, for example, in the structure of a scientific or clinical meeting on cancer. Those with contributions exclusively relating to normal cells will find themselves often segregated from mainstream symposia and relegated to a variety of intellectual ghetto slots in the meeting. Of course, this distinction, which is clear for solid organs, becomes obscured with the leukemias and lymphomas where there is often a need to replace pre-existing leukemic or lymphoma tissue by transplanted or selectively stimulated normal cells. Even here, a segregation is observable, although often in the not-too-disreputable form of an introductory session on normal stem cells or normal regulators and signaling pathways. Indeed, it is not uncommon in such meetings for studies on normal cells to dominate pathological or clinical studies—a reverse relevance judgment based on better current progress in one field than in the other.

For those taking the route of normal before neoplastic research, there are certain themes that are acceptable and those that are much less so. For example, contributions on cell proliferation or differentiation commitment are always acceptable on the quite proper grounds that these are cardinal abnormalities to be understood in neoplastic cells. What are often far less acceptable are studies on other aspects of normal cell biology or development.

We have used the scientific meeting example to illustrate some of the parameters for identifying what is being considered in the field to be of current relevance. However, there are other parameters that are familiar to all research workers where much the same judgments and criteria are being applied. These range from grant awards, to manuscript acceptance in journals, and even to the ability to have serious scientific communications with colleagues.

At the practical level, judgments on relevance coalesce to influence the most important single need of a research worker—the need to raise research funds. Money for research is either public money raised through taxes or money donated by private individuals. Both sources usually have in common the requirement that the research address a disease goal. It is much less common that the funding supports general biological studies with no identified goal. Precisely how broad projects can be and still meet the disease-related criteria depends often on the knowledge and perception of those administering the funds.

Success in grant applications is critical for most workers if they are to have adequate research funds for carrying out their proposed research. The assessment of a particular grant application is usually made by a grant committee composed of one's scientific peers. Most of these committees do their best to function in an unbiased and intellectually honest manner and are a credit to our society in what is a mentally exhausting and stressful voluntary activity.

Genuine differences of opinion can be held within committees regarding the relative value of short-term funding for many, versus long-term funding of a smaller number of groups. Fundamentally however, grant committees make two decisions—one regarding competence and one regarding relevance. Properly excluded under the competence criterion are projects of poor quality or design, projects that are unrealistic, duplicative or quite unlikely to result in reliable information of any type. The relevance criterion may be dictated in a very restrictive manner by the funding source, but more often will reflect the attitudes and experience of those on the current selection committee and these parameters will closely resemble those being used in the committees designing scientific meeting programs.

In principle, a grant application could be assessed solely on its apparent quality, but this judgment needs familiarity with the state of that field as assessed from published literature, including the applicants' own publications. In this regard, the quality and innovativeness of the applicants' prior publications, and, in particular, their impact on the field as indicated by citations, become important parameters for assessing not only the likely quality of the proposal, but also its perceived or likely relevance for the field.

Some very curious behavior patterns are involved in the publishing and citing of scientific papers and, because of the importance of publications and citations in determining funding, career advancement and perceived relevance, these patterns warrant some discussion.

	Publications, Citations and Relevance

Top Parameters for Assessing... Assessment of the Perceived... Publications, Citations and... Methods for Sustaining Relevance Conclusions

 
Aside from possible achievements as a teacher or mentor of younger scientists, the major product of a research worker is published papers and it is on the quality and quantity of these that all else depends. Major discoveries, however significant, are not independent entities. They do not exist until accurately recorded in a published form that is available to others. This is the social covenant entered into when accepting financial support for research. The usual vehicle for completion of this covenant is a scientific journal in which the research is published in the form of a scientific paper.

The impact of a published paper might sometimes be assessable by the changes it leads to in treatment or in the development of a new scientific field of inquiry. However, these are rare consequences and, in most instances, the impact and perceived relevance of a paper are revealed by the number of citations this paper generates in the publications of others. This could in principle result in an extraordinary situation if, for some reason, a particular scientific paper fails to come to the attention of others and therefore fails to be adequately cited. A major discovery may well have been made and documented in published form, but without acknowledgment and recognition by citations, the discovery has no real existence.

With citations being the real driving force behind a career that is successful or otherwise, it is alarming that most scientists construct lists of citations in a manuscript in a fairly cavalier and often reprehensible manner. There is no question that the preparation of such citation lists is a nuisance when writing a new manuscript. What is uppermost at the time is the presentation, analysis and discussion of the new material being described in the manuscript. References in such a manuscript to the prior or related work of others is an expected formal courtesy, but the papers quoted and discussed are likely to be those that agree or disagree with the observations being described, not those that are merely of general relevance to the subject. Self-citation is rife, as is skewed citation of the group's work or that of friends of the investigator. As noted above, publications older than two years commonly are not cited and there is a variety of additional dishonest maneuvers such as failure to cite relevant prior work on murine cells if the system being studied is identical, but uses human cells. In truth, in recent years, citation patterns have become the subject of many complaints because of their incompleteness or distortion of the literature, but referees rarely reject such manuscripts because of incomplete or biased reference lists.

In stark contrast to the often cavalier generation of reference lists and, thus, citations, authors go to extraordinary lengths in attempts to have their manuscripts accepted by journals whose papers generate more than average numbers of citations. This subset of super-journals has been established by the referencing pattern of the scientists themselves. Currently these journals include Nature, Science, and certain more specialized journals such as Cell. The reasoning behind the increasingly desperate attempts to achieve publication in these scientist-elevated journals is that acceptance is perceived as being tantamount to a vote of confidence that the paper was of superior quality, importance and relevance. In turn, the paper is more likely to be cited, facilitating successful passage over the hurdles a scientist must negotiate in his or her career.

Tagging along behind these superstar journals is a well-defined group of quality journals, maintaining top standards and dominating their respective, more specialized fields. There then follows a larger assortment of journals ranging from the quite acceptable to the terrible, in which published papers tend rarely or never to be cited.

What is of interest in this system is that, with the exception of journals published by specialized scientific associations, the majority of journals are commercial enterprises run for profit and with no consideration for public benefit. Scientific authors, in fact, labor without fee to produce, and have grudgingly accepted, manuscripts that will result in profit for the publishing company.

Despite the dubious nature of this arrangement, the system works well enough in practice because of the voluntary work of the scientific editorial board and manuscript reviewers who attempt to ensure truthfulness, accuracy, balance and technical adequacy in the publication. The system is reliable enough not to overlook novel or important discoveries or, at least, not miss them too often. For many journals, however, referees are asked specifically to assess the relevance of a manuscript—a parameter that is not necessarily related to novelty or importance. This relevance assessment is often masked under the euphemism of assigning a publication priority. Here, editors and referees have the anonymous capacity to accept or reject a manuscript, the prime mover of a scientific career, on grounds of relevance or priority that cannot be quantified and need not be justified.

Personal opinions on relevance and publication priority can have wide-ranging consequences according to the journal involved. It is self-evident that a submitted manuscript on lung disease would be considered irrelevant (inappropriate) for a journal with a scientific brief to publish contributions on hematology. This is quite proper and makes for an efficient preliminary sorting of the progressively expanding mass of published information.

Where some curious behavior patterns have arisen are with general scientific journals. Here, manuscripts can be rejected on the grounds of "insufficient general interest." But who decides what is of "general interest?" This decision can be made solely by unelected employees of a profit-making journal, but is aided all too often by scientific referees who use this convenient expression to pass judgment on a quite respectable contribution but of no particular importance to the referee concerned. Sometimes, by applying this phrase, the referee may well be wishing to appear more perceptive than others, possibly with a future manuscript of his own in mind for the same journal. Quite clearly, the term "insufficient general interest" can be applied to almost any contribution. A manuscript announcing a cure for cancer might well be of interest to all readers. However, one solving the nature of a signaling pathway in a cell may be of enormous importance to cell biologists but is of no possible interest to a taxonomist, an astronomer, or a mathematician.

The rubric "insufficient general interest" is therefore a convenient stratagem for reducing the number of submitted manuscripts. However, because some from each field must be allowed to survive, it becomes the subject of one or two individuals' private assessment of what subjects they consider to be currently fashionable, or, regrettably less often, as having made a significant advance.

Earlier in my career, in a surge of nationalistic individuality, we were encouraged to publish our papers exclusively in Australian journals. This would now be regarded as citation suicide and a sure pathway to continuing irrelevance. Some of my better earlier publications were indeed in these little-read Australian journals. Apart from guaranteeing obscurity, the most positive benefit was that in lecturing, particularly in the U.S., it was always easy to come up with novel data—not new, but novel to the audience. It would be idle to suppose that even with today's electronic access to the literature, this situation has changed in the slightest.

In later years, I have often chosen to publish papers in appropriate rather than in fashionable journals—appropriate being defined by me as a journal capable of prompt publication, doing a quality job of publishing and likely to reach my intended audience. Given the insular reading habits of U.S. scientists, the most numerous of my colleagues, this too is a recipe for disaster if one wishes to remain in public view and thus, via citation, to be considered relevant.

With this past record of intransigence, why should it now concern me when I perceive my manuscripts becoming (or continuing to be) categorized as irrelevant? In part, it is likely to be merely punctured pride, having had on previous occasions some relevance. In part, times have changed. It was acceptable in previous years to behave in a somewhat idiosyncratic manner when working alone or with a small group. Now the scene is different. The required technology or expertise is more complex, more expensive and demands group effort. What is at stake now is a group's reputation for excellence or relevance in what they do. This is not a scenario in which idiosyncratic behavior is appropriate and conformity in behavior is almost mandatory.

What we and our colleagues are now locked into is a self-perpetuating cycle. To be publishable, work certainly needs to be of quality, but it also needs to be considered relevant. These same publications dictate in turn what is considered relevant and therefore publishable. In this fairly inflexible pattern it becomes increasingly difficult to break new ground. Novel work has always been regarded with suspicion, often correctly, and initial publications are difficult to have accepted, with subsequent contributions on the subject becoming progressively easier. The vicious circle can be broken, but it does appear to impede overall progress in science.

Where real difficulties arise is where interesting phenomena are uncovered but are not of major importance and possibly are not able to be expanded into a significant stream of work. I have always been prone to spending (? wasting) time in these little forays into intriguing blind alleys. I do not regret the time lost on such little journeys, but can certainly attest to the fact that such material was always difficult to have published and now may be impossible. The almost invariable referees' responses, even 30 years ago, were of puzzlement. What motivated him to do these experiments? What is their possible relevance? I was often hard-pressed to come up with a response to these reasonable-enough criticisms. Indeed, it is a compliment to the former tolerance of journals that the material was ever published. Almost certainly, the publications were never cited, but was the information useless? The observations were accurate and reproducible and one day an explanation for them may emerge. For example, why does the mouse thymus atrophy during pregnancy? No doubt this occurs because of hormonal perturbation and possibly elevated corticosteroid levels. So far so good, but why do thymus grafts in the same animal fail to atrophy when they have the same cellular composition and general biology as that of the host thymus? This is a never-quoted, but nevertheless properly published study. By what criteria should this observation be considered irrelevant? Because it has no current explanation? Because nobody was prompted to follow up the observation? Because it was not a conceivable real-life situation?

I suspect that a major determinant for labeling a study relevant or not is whether research on the subject was continued. I would now be the first to support the view that persistence in a field is necessary to achieve significant advances: the colony stimulating factor saga at last brought home to me the reality of how to achieve scientific advances. Nevertheless, I regret the passing of the era when one could spend a little time on the many curiosities encountered. It cannot be entirely bad to have an inquiring mind and an eye for what is novel. Surely science always needs to be primed by such observations even if their attrition rate is high. It seems to me that the current demands for relevance and conformity lead to major resources being placed in monolithic enterprises. While this clearly can allow major advances, the practice at the same time artificially constrains the making of truly novel small discoveries that may prove vital in future work. Such novel small discoveries will be lost, of course, unless people are prepared to spend some time reviewing, citing and acting on earlier publications.

In this context I must admit that reading some of my own earlier publications has given me cause to reflect on phenomena now forgotten even by me that would repay some careful reinvestigation using more modern technology. I am sure that my own publications are not unique in this regard. All of us have little treasures of recorded or unrecorded past observations worthy of re-airing. Wouldn't it be nice to have a journal prepared to publish in note form this miscellany of intriguing past observations?

Because most of my current work is carried out in the form of studies by our group, assessment of the perceived relevance of the various projects really represents an assessment of the group projects. What is the relevance status being accorded to these projects, as indicated by the fate of our submitted manuscripts or grant applications? Again, the assessments being made give mixed signals. We often, but not always, fail with manuscript submissions to super-star journals. Usually, with persistence, our material gets published in top-quality, more specialized journals. On these grounds, the work of our group is being judged as being reasonably relevant, but perhaps not super-relevant. Most of our grant applications, eventually, are successful enough, again suggesting that our work is probably considered relevant. However, I suspect we may have currently declined in our citation impact, with a consequent decline in visibility in meeting programs.

It is always difficult to judge the origins of such fluctuations. In part we are victims of cyclical scientific fashions; in part our key younger scientists have yet to establish their reputations; in part we have entered a rather different field whose scope is not yet clear. The personal relevance of individuals in a research team is therefore determined to a significant degree by the current status of the whole group and measures to improve personal relevance in part depend on maintaining the status and perceived relevance of the group.

	Methods for Sustaining Relevance

Top Parameters for Assessing... Assessment of the Perceived... Publications, Citations and... Methods for Sustaining Relevance Conclusions

 
Accepting that there is such a thing as perceived relevance both at a personal and group level, that it is a judgment with potentially serious consequences and that there are parameters for identifying one's current status, what should be done about the matter if, as an elder scientist, perceived relevance seems to be in decline?

Being a realist, I am prepared to accept that a certain loss of relevance is age-related and therefore inevitable. I suspect, however, that the remaining loss is not age-related and can happen to anyone. I therefore do not believe that the correct overall response is to accept such judgments passively or to regard them as irreversible. All of us are only as good as our next experiment and the problem needs to be addressed in an active manner.

Retaining Personal Relevance
Technical advances tend to make all of us become outdated sooner or later. With time, more and more techniques become established in which we have no personal experience on which to draw for problem-solving or for generating ideas. To become outdated in technology and its related concepts and possibilities is probably the most common origin of a slide toward irrelevance in daily scientific life. This may not be entirely preventable, but it can be minimized if work is continued in a team context.

The cardinal thing to be avoided is to cease active laboratory work. This is the guaranteed pathway to irrelevance. It is also critical to remain master of certain techniques, to simply be better, more reliable or faster in executing these techniques than anyone in the group. This technical expertise, coupled with experience and a willingness to employ these techniques where they seem useful to a group project, contribute things of obvious value to a group and earn the right to be regarded as an equal, regardless of age.

It is somewhat bizarre to observe the progressive reduction in the age at which scientists choose, or allow themselves, to abandon bench work. When I started in research, 60 was the age at which scientists began to taper off their personal experiments. Today, the age is probably below 45. If one accepts the reasonable view that it takes 10 years to become competent in a discipline, then by 35 or 40 an investigator has only just become competent, although not widely experienced. It seems an extraordinary waste of this technical expertise to have that individual then retreat to an office and pass the execution of laboratory studies on to a partly trained post-doc or a barely trained Ph.D. student. The phenomenon is too new to predict the future consequences for these 35- to 40-year olds when they reach 60, but I find it difficult to imagine a scenario in which they will remain relevant. They can, of course, collect the result slides of their post-docs and students and still present a passable lecture, possibly even without too many injured feelings. However, I would hate to have them working by my side at the bench on a difficult technical problem.

Although, intuitively, it might not seem likely, a strong defensive maneuver for retaining some vestiges of personal relevance is never to leave the particular field in which one initially gained prominence. Sustained work for decades on a particular subject does seem to confer a certain continuing level of attention and relevance on some individuals even though their perceived relevance may in part be dependent on advances by others in this narrow field.

One might imagine, therefore, that a foolproof method for sustaining reasonable personal relevance is to keep making discoveries in one's familiar field that, if not world-shattering, are at least thought-provoking and substantial. There is, however, a definite phenomenon of star fatigue. After a time, colleagues tire of acknowledging yet another contribution from a productive colleague. We all seem to need new faces to admire.

This phenomenon becomes quite apparent when the increasing complexity of a subject necessitates attack by a more or less stable team of investigators. Although a formerly prominent worker may continue to play a key role in the productivity and success of the group, attention switches almost inevitably to the younger emerging stars in the group. This is, in fact, the rationale and strength of group work. The work of junior colleagues is not buried in the team but, to the contrary, teamwork accelerates the rise to prominence of younger team members.

To single-mindedly pursue the familiar, if now currently unpopular, is a fairly austere prospect and one likely to result either in solo experimental work or, at best, work with a very small group. This particular pathway may not lead to major discoveries, but it does allow a certain freedom to pursue the novel and potentially important. This may well be a fairly lonely pathway where the rewards are in the joy of minor discovery, not the acknowledgment of discovery.

Any discovery has value, provided it is accurately and thoughtfully recorded. Experience indicates, however, that the loss rate of isolated observations is high, despite the existence of electronic data retrieval, often because the title and abstract do not reveal the pearls in the results section. It is this loss of accrued slivers of information that renders the work ineffective and carries with it the harsh judgment of lack of impact, lack of influence or lack of relevance for the unfortunate author.

Retaining Group Relevance
I prefer to undertake most of my work within the program of a multidisciplinary group on the grounds that such a group is more likely to achieve major advances. However, as an aging member of the group, one can no longer expect to have much influence on the choice of subject to be pursued. If others view the subject chosen by the group with indifference, then it is up to all members of the group to prove the judgment mistaken.

Even with a strong initial discovery capable of being exploited by a productive group, success and recognition are not guaranteed, nor will the recognition of this success last more than two to five years. This is the pressurized world of the big battalions with high stakes and possible expensive disappointments. The group may dissipate its resources and perceived relevance pursuing minutiae or blind leads. The rules for disengagement from such unproductive work need to be agreed to early by all group members and, more difficult, adhered to. The necessary hard work needs to be sustained, no opportunities overlooked and a very watchful eye kept on a carefully orchestrated publication sequence in appropriate journals.

There is no place in this method of research for repeatedly following leads uncovered by others. Such leads will certainly either be actively pursued by the originators or by groups eager to be seen to be working in an active field. The latter may not be particularly formidable competitors, but their sheer numbers will result in many of the possible avenues of development being pre-empted. There may be occasional exceptions to the rule against "copycat" science but, on such occasions, the group's past activities and experience need to confer some major competitive advantage. The risk remains that any results achieved will likely be regarded as derivative rather than innovative.

This manner of undertaking group research may seem hard-nosed and to have little regard for the value of an individual's spirit of inquiry or joy of discovery. However, the approach is goal-oriented and has at least the potential to elevate the work from the level of individual curiosity to a level where the discoveries made have some realistic possibility of practical application. Most discoveries have this potential, but it does require deliberate planning to pursue a discovery with the serious objective of developing the discovery as far as current science or technology permits.

Given sustained effort, intelligence in choosing an appropriate program for exploration and reasonable good fortune, a group can generate its own subdiscipline and its consequent perceived relevance among its colleagues. Relevance then becomes something that is creatable rather than a passively conferred judgment.

	Conclusions

Top Parameters for Assessing... Assessment of the Perceived... Publications, Citations and... Methods for Sustaining Relevance Conclusions

 
Whether we like it or not, judgments on our relevance are being passed on us by our colleagues on an almost daily basis and do influence our ability to undertake research.

To be judged irrelevant can have some serious consequences, and it certainly places us outside the normal range. How we respond to this judgment will depend on our individual characteristics. The pessimists among us will assume that they are in the lower range of the normal curve and retreat from laboratory life. The optimists and recalcitrants may feel that they are now free of some of the restraints of the normal range. Avoiding the pitfalls of becoming an eccentric crank, an individual may seize the opportunity to engage in personal research in quite novel areas. Alternatively, one can simply respond to the judgment by helping ensure that the achievements of the group in which one works are so superior that the present judgments are rendered fallacious.

Within the limitations of our ability to influence our own fate, our future and perceived relevance lie in our own hands.

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