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It has been over a decade since the introduction of the word proteomics (1), and some suggest that the last 10 years has seen us fall way short of delivering on its potential. Others claim that too much was promised and expected in the first place. It is therefore timely to examine what has been delivered and perhaps to redefine the promise of proteomics and related omic strategies. It is also a good opportunity to assess the important elements of omics submissions that might be published in journals such as Experimental Biology and Medicine.
Most life scientists operate in an environment where data are hard to come by. They have been trained to construct focused, falsifiable hypotheses, to test one or a couple of variables at a time, and in this manner to incrementally advance our knowledge of a specific issue. By contrast, omic techniques offer the potential to interrogate thousands of independent variables in a single study, and thereby promise expedited approaches to advancing biofmarker discovery, identifying novel drug targets, and understanding the underlying mechanisms of health and disease. But are we applying these methods appropriately, or are we simply enamored with these tools to the point where we have lost sight of the biologic imperative underlying the work? Have we equated the acquisition of massive data sets with the practice of science believing that biomarkers, therapeutic targets, and mechanistic insights would flow from these studies like water from a fountain?
Our scientific colleagues in other disciplines would attest to the fact that observation and measurement are major components of the scientific process but that data acquisition does not equate to knowledge acquisition. After all, people have been "looking" at thousands of variables for centuries (including biologists, astronomers, and geologists), but precious few have been blessed with the insight to advance novel, falsifiable hypotheses, test them, and then repeat and refine the process.
To my mind, the most critical issues as they relate to the application of the omics methods in experimental biology and medicine can be summarized in a few key points.
Perhaps at different points in time and in response to different circumstances, scientists should revisit some central issues. In 1964 John Platt wrote of "strong inference" (2): i.e., (i) devising alternative hypotheses; (ii) devising a crucial experiment (or several of them), with alternative possible outcomes, each of which will, as nearly as possible, exclude one or more of the hypotheses; (iii) carrying out the experiment so as to get a clean result; (iv) recycling the procedure, making subhypotheses or sequential hypotheses to refine the possibilities that remain; and so on. Building on the works of Bacon, Popper, and others Platt defines these steps as critical components in the scientific endeavor.
We need to remember that the omics methods do not profoundly change the scientific process. The great value of these data, just like the images from an interplanetary probe such as Hubble, is that they offer a powerful alternative first step to hypothesis generation because they are independent of existing knowledge and less dependent on insight, instinct, and experience. A single omics study may present us with data from which we can formulate dozens of testable hypotheses and, as T. C. Chamberlin suggested (3), when we have multiple lines of independent investigation, it limits our potential to embrace a single hypothesis with too much affection, to press our theory to fit the facts and to press the facts to make them fit our theory. Multiple independent hypotheses therefore help us to be more objective, to distribute our effort and divide our affections. Each hypothesis then suggests " . . . its own criteria, its own means of proof, its own method of developing the truth, and if a group of hypotheses encompass the subject on all sides, the total outcome of means and of methods is full and rich" (3). But, as Platt suggests, each hypothesis needs to be investigated: no corners can be cut; no alternative explanations of the findings overlooked.
The omic methods will be powerful aids to understanding biology and advancing clinical practice, but it was never going to be as easy as some led us to believe. The early promise we offered our colleagues, collaborators, and granting agencies was false—a few months’ work and a couple dozen retrospective collected samples were never going to deliver a handful of markers ready for routine clinical application. Highly specific and sensitive markers do not fall in your lap; rigorous testing is required. Scientific investigations over the centuries prove that: (i) there is no substitute for formulating, testing and retesting falsifiable hypotheses; (ii) we must eliminate the potential for bias and chance to confound our studies; and (iii) we must have an intimate understanding of the quality of our data and the sources of errors associated with it.
In summary, as we generate our data and prepare it for publication, we should not forget the principles that underpin science and the tried and tested approaches to advancing knowledge. We need to ask good questions; design and conduct good studies; define the limits of our methods; interpret our data in an honest and objective manner; and, wherever possible, we should offer alternative explanations for our observations. No study will be perfect. We will rarely deliver the bottom line (e.g., validated biomarkers), but elegant and well-conceived studies should be our goal; massive, overly ambitious studies are more likely to confound rather than advance our knowledge.
References
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