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 An intelligent person would never go to war or start a business without careful analysis of the factors above, yet most research planning gives them only brief attention. Usually we are so immersed in the details that we neglect the broader concerns. We may even claim that we are so busy doing that we don’t have time for esoteric planning. Careful planning of an experiment determines its value. If most experiments were to begin as a ‘gedanken’ experiment, a thoughtful anticipation of the likely progress and outcome of the experiment, then the few that are physically undertaken would be more likely to be key experiments. “From the way a war is planned, one can forecast its outcome. Careful planning will lead to success and careless planning to defeat. How much more certain is defeat if there is no planning at all!” [Sun Tzu, ~500 B.C.] Failure to consider the factors above creates some of the more common experimental pitfalls: “The winner does everything to ensure success before he fights. The loser rushes into combat without adequate preparation.” [Sun Tzu, ~500 B.C.]
 * underestimating the amount of time that an experiment will take. Underestimation is most acute when the planned experiment has never been done before (e.g., when one is designing new equipment for a novel experiment). Almost always, one’s overall time estimate is much shorter and less realistic than would be an estimate based on a list of the time requirements of individual steps. Most experimenters also fail to include time estimates for delays, setbacks, and unexpected problems, and their time estimates assume ‘production mode’ rather than the entire period from set-up to shut down. I routinely allow optimism to carry me into this pitfall, even though I recognize the wisdom of my wife’s rule of thumb: carefully estimate the time for each individual step, sum these times, and then double the total.
 * lack of time management, resulting from taking each step as it is encountered. For example, running batch processes is usually more efficient than doing experiments in series. The wait time that occurs somewhere in most experiments can often be filled with another part of the experiment, if the process is planned as a whole. If I concentrate, I can keep three processes going at a time.
 * lack of strategy. Even a tactically brilliant project can be strategically ineffectual or foolish; the best example is the Japanese attack on Pearl Harbor. The consequences of clever implementation of unfocussed research are less drastic: inefficiency and ho-hum science. Many ingenious experiments contribute little, because of insufficient attention to overall strategy. Too many experiments are selected merely because they are obvious or logical follow-ups to previous experiments. A more powerful selection strategy is to consider various possible experiments, then select the one that is likely to contribute most.
 * lack of risk management. Often, surprisingly small changes in design or technique can profoundly affect the value of an experiment. Yet these refinements are neglected, because planning is short-circuited by optimism, lack of risk analysis, or enthusiasm to get started. In hindsight, the changes that should have been made are obvious.

Observational versus Experimental Science
Many scientific disciplines are more observational than experimental. Within these research areas, only a few of the guidelines for experimental design in this chapter will apply. For example, in observational or descriptive branches of biology, ecology, psychology, anthropology, and astronomy, manipulation of variables is not always possible. With many natural phenomena one cannot