When I talk to someone, I want to know about them, not about the weather or the trip to work. I'm not much at "social conversation" but at least I know the difference in gaining knowledge about a person and relating. We may not agree on the nature of the difference, but there is one.

I want to know things, whole things. I can look at your nose but I prefer a little distance so I can see your face. There is meaning, proportion, beauty, and relevance in the context of things - noses, nuthatches, and analyses. There is much to be known about knowledge, as discussed in the previous chapter. This chapter is about gaining knowledge, creating a knowledge base. The typical modern view, at least one promoted in the modern university, is that much knowledge comes from research

Research, if well done, is done scientifically, and thus there are strong relations between science and knowledge. I seek to achieve a new balance in the world of known relations and descriptions. My view borders on anti-science, but it is not. It suggests, merely, that "science" not be so outspoken and that it take a mannerly place at the table with the other members of the knowledge-base-building world.

Since Sputnik, science has been dominant. It invaded every corner of the university and scholarly world. Every discipline, to get money or status, had to do things in a scientific way. The difficulties were great; the pain inflicted intolerable for some; the losses were inconspicuous in the bright successes of enormously funded projects well promoted.

Science was research. Knowledge gained seemed to emerge from experiments and tests. If knowledge did not emerge from the bowels of real science, it did not exist or had little worth. "To know" anything, a person had to have gained it from induction.

I over-simplify, of course, only for brevity and clarity. The point is: within the natural resource fields we badly need knowledge. Our need is to gain, store, retrieve, use and revise knowledge well. That is a very tall order. We need an entire knowledge system, not just "studies." Science is one way to gain knowledge, but only one way. No matter how good it may be, it is not exclusive, may no longer be allowed its exclusivity, at least among the natural resource fields. There are many ways to know; science is only one. Research is only a part of science. The pathway I create, the trail I dig around a rocky hillside, is one of truth-seeking, knowledge-base-building, not just "doing science."

I have no special claim to knowledge about what is good research, but I think I know about knowledge needed in the natural resource fields, particularly the wildlands. Thus, I appreciate studies that tend to gain such knowledge. I have a limited view of what studies should be conducted because studies are so enslaved by methods that their objectives are often compromised. The same can be said about who should do such studies. The student and the procedure overpower the purpose. There is a looming need for knowledge among the natural resource managements. Not research per se, but knowledge. Damn the source!

In the present, some 50 years more of it, I see severely limited funds for studies, limited facilities, few researchers with direct control with use and users of resources, and almost none with a systems orientation. That may make little difference unless the context of expanding human populations, shrinking prime land, reduced fossil energy availability, and increasing contamination is perceived. We have no more time. The scientific paradigm of study, report, and someday-somebody-will-usethe-results-in-some way is pass&#eacute;. It was nice, interesting, useful, quiet ... but we are in a new situation. The old scientific approach (long-live the approach among a few) is no longer adequate. Perhaps it never was, but many people of reputation asserted its dominion and essential in society. It seems inadequate.

We need to develop a procedure for building a knowledge base. Classical science can continue its contributory role. We need an orientation that studies of all types should yield pre-stated inputs to decisions about actions that managers may take to improve conditions or (to stabilize a system at some desired level ). The outputs of research are inputs to decisions. The outputs of wildlife research, for example, cannot be "publications" or "filed reports." The outputs are not to be rediscovered years later in some monastic field station file cabinets.. The problems of the wildlife resource are now. The situations with hundreds of species world-wide are those of crises. If necessary, the phrase "applied research" may be used as the category of need. This misses the point. It suggests the other side, "basic research", of that same wafer-thin coin. Both types exist and are needed, but in the realm of natural resource management, I see no justification in arguing for basic research with my understanding and observations of the present world. I can only insist upon highly applied work, seeking answers about what to do, what actions to take, what combinations to employ. What effects can be expected from a treatment? The needs are akin to those in modern animal husbandry. The objective is net benefit. Users of fundamental knowledge, faunal system managers, cannot ever amass the funds needed to study the biochemistry of energy bonding and energy loss from cells of animals in desert conditions. Interesting, yes; but if pure truth were available, what would the manager do with it? Several souveniers of my trips to India were once at Peculiar Manor. There are few wildlife managers in India but their questions need immediate answers:

How can people be gotten to experience wildlife safely and with minimum effect on the desert?

What is the demand for experiencing desert wildlife? For example, the endangered onager of the Rann of Kutch. Can it be increased?

Can water catchments improve conditions? Will catchments increase range use and thereby destroy critical habitats?

Can built windbreaks improve habitats for desert animals?

How can mortality of young be reduced?

How can poaching be stopped?

Is damage caused to crops by animals feeding at the edges of deserts? Can it be reduced? Compensation for loss afforded?

Can breeding occur in captivity?

The list can be much longer, but it is noteworthy that the last topic can cause the wildlife manager to careen off along a research pathway that hardly looks as if it is applied. (Every question has this node from which branching may (and tends to) occur.) The need for breeding animals in captivity is evident when endangered species are considered. Why there are failures (behavioral), whether hormones may be used (endocrinology), whether high energy diets will induce egg production (nutrition and reproductive physiology), what are the hazards of inbreeding, and what are minimum numbers from which populations cannot recover (genetics), all sound like good questions, quite basic, and probably useful when each conclusion is reached.

I view these as fundamental studies. I believe wildlife managers should encourage others to do them. They are relevant to a few hundred out of about 10,000 species with which managers may work. Those few species have great value, so there is full justification for wildlife management research doing these studies after failing to get assistance from others, who are probably better qualified and equipped.

I do not know who should do what type of studies. There are hundreds of zoologists. Some just happen to study large wild animals, not wild millipedes or tubellarid snails. It is important that these studies be done and done well, but herein I suggest that all people who study wild animals are not participating in wildlife management. There are parallelisms in other resources. I do not wish to draw artificial lines. I do draw one, though, and that is done to solve questions of allocating funds, time, and expertise. The needs that exist are akin to advances made in agriculture. The fundamental question is: if I do X or change Y, what will happen to the animals and the potential net benefits derived from them? Other questions are for someone else, not those engaged in the complex, total system of resource management.

I believe some wildlife funds should be spent on basic research, that which answers questions just because they are there; that which serves curiosity, that for which the answer to "why do it?" is "just because!" The amount should be less than one percent; the reason for it is to encourage the mutant idea and to retain a variety of potential inputs to a knowledge base. The reason for why not do more is simply - we cannot afford it.

I believe that by taking a systems approach to natural resource research, the 6 competing perspectives of that pattern (context, inputs, processes, objectives, feedforward, and feedback) provide a totality and diversity unseen in any research community. I have suggested elsewhere that a species-specific approach will not work. There are too many species; we will never finish; too few experts, too many areas, too little money. It is irrational to act as if we might. (Rational people are opposed to irrationality.) An alternative is to take more fundamental pathways - photosynthesis of forage and cover plants, convective heat losses of animals, inhibitions by toxic substances, costs of movement.

Eventually someone reports that they know the effects of solar radiation on a key food plant of wildlife. Now ... where is the knowledge about how much radiation from what spectra are available in a specific site of managerial importance? The measurements have not been made in the past. It is not feasible to collect data for three or more years to get a good average ... even if the equipment could be afforded for that and 50 other sites. What to do? What to do? This is the manager's question and unless all of the answers to the set of decision questions, the decision will be delayed or made poorly. I believe that there is a type of action needed - one that is seeking fundamental chunks of knowledge that are answers for such questions. I see needs for models to be developed that allow site-specific estimates to be made of the non-biologic, the abiotic, parts of the natural resource world. These are grossly deductive, but unify knowledge from any source. Rainfall, temperatures, precipitation, solar radiation are examples. There is a general assumption that these commonplace words have data readily available to do with them. Not so! The rainfall record from the nearest weather station may have little relation to rainfall at a forest, mining, or fishery site (e.g., a feeding, nesting, or migratory resting area). Equations exist for solar radiation on a flat surface on a cloudless day. The wildlife manager planning for 20 years on a site on a northwest-facing slope of a large mountain wants to know the likely radiation of a spectral range that allows differences to be explained in plant survival, size, and energy content for foraging creatures - all 500 of them.

There are ways to compute such relations, but knowledge that there are ways is as functionless as not knowing there are ways to do so. Ease of use, accessibility, is as essential to having knowledge as having good research procedures. There is no way to measure every relevant factor on every site requiring a decision. Estimates are needed and the complexity of each natural variable is such as to require a computer model to make an estimate, or for the manager to be wrong. Both conditions produce an action (a usual condition and one very likely suboptimum or dead wrong.) There is a big difference between being approximately right and precisely wrong.

Somehow studying the hours in which nighttime brightness from the moon exceeds a pre-determined amount does not sound like wildlife management. It could have been done, probably for centuries. It is a study that produces a number for a site, that allows a manager to explain the difference in predation between sites, allows invertebrate behavior to be explained and related to their role as prey, and allows a decision about where funds can be spent to get desired animals or where desired numbers will be produced naturally ... without investment. We need knowledge, to know where it is and how to get it ... on time, at low cost. Somehow, these same words are used to define any resource.

Values of people are said to be subjective. Objective research can be conducted on human objectives and on the numbers they assign as expressions of relative importance of wildlife. Not the animals, but the people, are the target of the studies. The wildlife management researcher is as likely to study people, as plants, as animals. How peoples' values change with age, cultural differences among groups, how religion and socioeconomic condition influence assigned weights (indexes to their relative value estimates) are reasonable, applied studies. Perhaps they can be considered to be inventories. I view inventories as raw data collection that must be converted by systems-oriented people into inputs to some specific decisions. Secondary use of inventory data is an extra benefit. The inventory must be justified on the grounds of cost per conclusion, an entry into the knowledge base, or cost per summary statistic actually used in decisions.

This work on people, on moon forces, and on inventory results all sound very abiotic. Most wildlife managers get into the business because they love animals or have experienced beautiful scenes and stories on television. The fate of wildlife is not in the hands of zoologists learning more and more about wild animals. Some of their studies may be used by wildlife managers and they will be thankful for their work. The genuine challenges ahead are for practical, hard-minded people who love wildlife but who are willing to work with the issues needed for the wildlife resource, not with the topics of interest and pleasure to them personally.

I struggle to comprehend the new science, the replacement of a largely inductive approach to knowledge about wildlife. Already mildly deductive, the new approach replacing "science" must become even more so, using general knowledge to solve particular problems on different sites in new ways. There has to be more risk-taking as the pressures increase for solutions that are timely, site-specific, and for unique problems.

My solution is called the Gamma Theory knowledge-base paradigm, for it is not deductive, inductive, or any of the conventional procedures, or the so-called dialectic between the two. I see a 20-compartment paradigm, not easily taught or easily tested-for on a multiple-choice test, so it will probably never enter the university or the minds of their B-minus student graduates now populating the resource agencies and their research arms.

The action components cast for analog in wildlife resource management are:

1. Clarify sets of objectives including dimensions of units of measure, demand, value, expected or probably achievement, variety of objectives, substitutability.
2. Clarify "publics" as each relate to the above and the causes of changes in these indexes over time.
3. Clarify time horizons of the publics, their perception of the importance of future generations, which may benefit from the resource, and appropriate planning and discounting periods.
4. Intensively use previous research and reports. A truly massive resource exists that can be harvested for a comprehensive database on natural resources and people.
5. Create entire analytical "packages" or computer programs using hypothetical or expected data before the first data are collected.
6. Create a set of theoretical models to allow estimates of major dimensions of wildlife populations, their habitat, and human use and response to wildlife.
7. Use expert knowledge and observations of field workers allowing them to express frequency of natural phenomena, maximum and minimum values, and likely median values.
8. Create a geographic information system that can estimate a range of values to fundamental ecosystem variables such as solar radiation, precipitation, temperatures, soil texture and depth, available key soil nutrients (N,P,K), and geomorphology.
9. Create a faunal information system with about 200 factors (or spaces) stored about each species.
10. Create a plant information system with similar "need-to-know" vs. "nice-to-know" data fields with connective interfaces to the faunal system and geographic system.
11. Create a community or ecosystem information base. Management decisions are made for forest "stands," about "ponds," and for burning a shrub-savannah. Without community knowledge, the linkages among the above systems are difficult, so highly unlikely. Each community has data on changes with age.
12. Use dynamic classification (Williamson 1981), a tentative, temporary, site-specific nominal grouping to meet local needs, given a particular context for a problem and decision.
13. Use simulation to discover ranges of change once a decision is implemented to detect intolerable surplus or shortages and to seek unexpected or counter-intuitive results. Results are typically expressed as benefit units generated, species abundance and richness changes, and changes in major resource indexes such as runoff, peak flows, standing biomass or commercial wood, fruit production, viewscape index change, stream sediment loads, and stored ground water levels.
14. Use optimization models with intense interest in the objective - including a full range of factors, and with little interest in great precision in estimates of the values. The emphasis is on the optimization process, whole systems building, and awareness of the likelihood that in wildlife systems once a solution is selected, there is likely a broad range over which it can be applied without violating the process. The system is often robust; success is not very sensitive to minor changes in the major variables.
15 Persistently use estimates of the future to revise solutions provided today. If a desired condition will result by nature in 5 years due to plant growth and community changes, then why invest money today to get equivalent food, water, or shelter in 5 years? The emphasis is on dynamic systems of changing plants, animals, and ... human objectives (in all of their dimensions).
16. Use small sample sizes, stratifying observations to reduce their variability, reducing required confidence levels for short-term situations, and broadening the bounds of tolerable error. Adaptive changes and adjustments can be made after further observations in most wildlife management situations. Few decisions are irrevocable, unalterable. Confidence levels of 10 to 20 percent are appropriate. Insisting on confidence of 95 percent in wildlife management decisions is an absurd disregard for the outstanding questions and the extremely limited funds and expertise available.
17. Use sampling strategies employing searching techniques and irregular intervals (contra conventional linear, binary, or bracketing intervals) in experimental design (Ackoff 1954).
18. Use daily or periodic data analyses to avoid the losses in time and money associated with unadjusted projects. Interim adjustments seen necessary and are made feasible by computer analyses of partial data sets and as they accumulate.
19. Exert efforts to break the hold of journal-article-publication on the field, replacing it with electronic media storage and retrieval systems, one-observation entries into databases, and progressive use of auto-regression and related improvements of statistics as more data become available.
20. Give increased attention to and rewards for team efforts in knowledge-base building and maintenance.

The nice, easily-remembered 6-step dance of induction called "science" must eventually be replaced with this 20-step Gamma Theory paradigm in a race for the long run.