Vol 50, No 2 April 2013

Mouse Medicine and Human Biology

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he choice of topic for this issue of Seminars in Hematology was stimulated by real life experience with editors, and being an editor myself I recognized an opportunity for redress (or revenge). Recent publicity1 concerning an exhaustive comparison of murine and human inflammatory diseases2 has made the issue, in both senses, particularly timely. The backstory. Editors’ responses to two of our papers were routine, even typical, but their implications are not mundane. The first manuscript described a mechanism of genomic instability, demonstrated in human tissue obtained from a patient population at risk for later malignancies. The work, unusual if not unique in the humble opinion of the authors, was returned without review, with the explanation, roughly paraphrased, being ‘‘we already knew this from mouse experiments.’’ The second manuscript, a report of a randomized clinical trial comparing two treatments, showed a marked, unanticipated difference in primary outcomes, including survival; the execution of this randomized controlled protocol was exemplary, the statistical analysis was strong, and the results had immediate importance for treatment of patients worldwide. However, the editors desired a ‘‘mechanism’’ to explain the differences. What do these editorial comments—familiar, reflexive, almost banal, and hardly extreme— signify? For one, they represent a gross undervaluation of work in humans, in these particular instances in extremely ill patients, in a research hospital setting lacking pharmaceutical industry support, and with onerous regulatory oversight: to be concrete, an ignorance of the pain of a biopsy and the

Dr. Young serves as Editor in his personal capacity. The views expressed are his and do not necessarily represent the views of the National Institutes of Health or the US Government. 0037-1963/$ - see front matter & 2013 Published by Elsevier Inc. http://dx.doi.org/10.1053/j.seminhematol.2013.03.024

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labor of adequately storing serial tissue samples; the effort of filing adverse event reports and amendments before an institutional review board; and the real ethical dilemmas inherent in clinical research. Second, such comments, disseminated among colleagues and especially young researchers in training, are a major disincentive to performing studies in humans. After all, if there is a mouse precedent, its demonstration in humans is to be expected and therefore to be relegated to the subspecialty literature. Despite the trendiness of ‘‘translation,’’ the primary language (expressed in data from animal models) remains primary and therefore monoglottal. Third, and most important, there must be a ‘‘mechanism’’: the clockwork must be revealed in order to trust the time on the dial. Establishing the putative mechanism in human studies often means choosing among diverse data for the correlation with the strongest associated p value or the most plausible biological correlate, neither of which has a convincing philosophical basis. Our statistical assumptions may be too optimistic or not empirically validated by replication,3 and biologic correlates in complex systems tend to be highly selective, influenced by the choice of assay to apply and even the pathway de jour. The accepted assertion instead is that any interesting finding in humans must be bolstered by a mouse model in order to be credible. But is this assertion really valid? Deeply problematic is the belief that all can be understood, at the level of the cell or organism. I intend here not just a warning against ‘‘hyping’’ results but an overestimation of the reliability of scientific data. In reality, much vaunted basic science is not reproducible in practice.4 Replication is extremely important but largely unrewarded as an isolated effort. So pharmaceutical companies have developed a healthy skepticism for academic laboratories’ outputs.4,5 Faith in obtaining that complete story (as represented by the typical gigantic cell paper) has had other unintended consequences, in enormously prolonging the process of publication, the length of training in biology, Seminars in Hematology, Vol 50, No 2, April 2013, pp 88–91

Introduction

and lottery like prospects for success in the sciences.6 Of course, the laboratory mouse is a wonderful creature—so well understood, so uniform in genetic and biologic characteristics, so tractable to manipulation—and so useful in establishing academic careers.5 But as a piqued colleague of mine once commented, he learns more about treating his disease from one indifferent clinical report than from anything murine published in the highest impact journals. So what do we learn from the mouse? A lot; the list is long, but certainly the mouse is an extraordinary discovery tool (of a gene, genetic regulation, a signal transduction pathway, a cell surface marker). But the laboratory rodent is much less helpful when things get complicated, as they tend to do in disease (in which genes, pathways, and cell membranes meet the heterogeneity of human genetics and environment). Experiments in the mouse can show biological plausibility, as for example that an observed correlation in human disease can be replicated under more controlled circumstances, sometimes even establishing causality in addition to association. Unfortunately, as is generally the case, positive examples (however representative) are extrapolated generally, negative data minimized or perhaps more frequently simply never reported7. How many murine ‘‘knockout’’ and transgenic models fail to reproduce the expected phenotype? Indeed, negative results in animals may be mislead or divert lines of research (for many examples in toxicology screening, see Shanks et al8). The laboratory mouse is the highest organism biologists can study using the reductionist approach. While many of the variables that hamper human studies can be identified and controlled in order to focus on a single factor, there are profound differences among mouse strains in physiology and disease susceptibility and manifestations, and, despite extensive inbreeding, considerable inter-individual variability within a strain (animals, even genetically simple ones in the same environment, have the inconvenient habit of dying over a wide time span even under the most controlled conditions). Elegant experiments in the laboratory mouse have led to profound discoveries. However, deep understanding of murine genetics, cellular and molecular biology has come at a cost—the artificial evolution of a strange animal developed over hundreds of generations of rigorous inbreeding, rigid diets, and infection control. That this deviation from nature may deserve study for its oddity, for aesthetic reasons, and to attempt to define normal physiologic states in reverse, may be appealing, but perhaps not to those who fund biomedical research. Although the recent public stir has concerned the demonstrated failure of the mouse model in sepsis, a

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decade’s systematic effort which, notably, was widely rejected by major journals before its ultimate publication,2 the problem has been extensively addressed in the literature for many years (see5,9–13 as a few examples among many). Unfortunately, sepsis is not the exception. The mouse has failed us in other areas: autoimmune syndromes and in immunologic processes in general,14,15 a wide range of neurologic diseases,16–19 and atherosclerosis,20 in a partial list, and sometimes with spectacular consequences in failing to predict drug and biologic effects on patients and even normal human volunteers.21 At least part of the problem of translation to humans relates to the poor design of many animal studies,8,15 including a variety of biases similar to or even worse than in clinical trials,22 Concern with inability to ‘‘translate’’ has been debated as a matter of public policy.23,24 A hematologist with a good memory will recall that L1210 leukemia was cured in the mouse decades ago and that result contributed mightily to the development of cytotoxic chemotherapy in the clinic; nevertheless, progress towards amelioration of the vast majority of human acute myeloid leukemia has been minimal. Conversely, remarkable advances have been made in blood diseases using empiric approaches only distantly related to caged animals, as in acute lymphoblastic leukemia. Metrics of success of a scientific approach may be very difficult—perhaps impossible—to establish and to test.25 We may not need to know the optimal way to do science; science has been a remarkably successful enterprise even when ‘‘Science’’ cannot be very easily defined. As my colleague John Ioannidis has shown, only a very small proportion of promising preclinical work published in high impact journals finds its way to clinical trials, approval, and usefulness to patients.26 Nevertheless, absent a normative, even a one or two percent success rate may be acceptable and perhaps superior to any other method. Likewise, that the mouse should prove less useful in modeling human disease than hoped or hyped is to be appreciated but not necessarily disparaged. A number is only a number, but a really low number might make us wince when we read of the next animal model’s promise—in the discussion, the editorial, or the newspaper—for understanding, ameliorating or curing human disease. Indeed, we do not have a very clear idea of the efficiency of science, or as in an economist’s term, the ‘‘returnon-investment’’ of basic research in general and of specific programs. The elegance of experimentation in the mouse, based on the enormous knowledge of the animals’ genome and genetics, their fixed environment, a vast number of historical studies dating back many decades, has led to a certain sense of intellectual

N.S. Young

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superiority, based on experiments that are often breathtakingly beautiful, but not justified to the extent that they may have limited correlation with the presumed targets of the (medical) research. And we might grimace at the preponderance of animal work filling the pages of esteemed journals purportedly devoted to ‘‘clinical investigation’’ and ‘‘experimental medicine.’’ (In this respect the mouse has been a particularly egregious model—for medical research itself—compared to which every experiment in humans will be deemed deficient!) There is some obligation to honest reporting and judgment, especially on the part of those who control the visible output of scientific work, the editors of journals. As has been emphasized, science authorities (hiring, tenure, and promotion committees, private donors and public funding agencies) have ceded signaling of success to a select group of journals and editors, who have different incentives than do working scientists.7 The editors depend on reviewers, of course, who for mouse work will be other experts in the (mouse work) field, with fairly obvious incentives. After all, there are alternatives (empiric clinical research, high throughput screening, molecular targeting of cellular pathways and cell–cell interactions, and others). Comprehending the relationship that links the scientist and his laboratory, editors, reviewers, and publishers, and consumers of scientific data does not mean that this complex structure should be dismantled, only that some skepticism and adjustment of expectations may be appropriate. Such a perspective may allow a clearer separation of the goals of biomedical research and the necessities of science as an enterprise. The collection of articles in the current volume offer a range of views of the utility and disadvantages of animal models in hematologic disease. Not surprisingly, those invested in mouse models may be reluctant to be too self-critical; those in the clinic may hesitate in the face of the esoterica of the animal laboratory and the complexity of even an individual experiment. Nevertheless, the articles are comprehensive, and their novel approach should be of interest to Seminars’ readers.

Acknowledgments I am grateful for thoughtful comments and conversations with Drs John Barrett, Alan Schechter, Cynthia Dunbar, and Christopher Hourigan.

Neal S. Young, MD Seminars in Hematology Editor

REFERENCE 1. Kolata G. Mice fall short as test subjects for humans’ deadly ills. The New York Times 13 A.D. 2. Seok J, Warren HS, Cuenca AG, et al. Genomic responses in mouse models poorly mimic human inflammatory diseases. Proc Natl Acad Sci U.S.A. 2013;110:3507–12. 3. Broer L, Lill CM, Schuur M, et al. Distinguishing true from false positives in genomic studies: p values. Eur J Epidemiol. 2013;28:131–8. 4. Begley CG, Ellis LM. Drug development: Raise standards for preclinical cancer research. Nature. 2012;483:531–3. 5. Horrobin DF. Modern biomedical research: an internally self-consistent universe with little contact with medical reality? Nat Rev Drug Discov. 2003;2:151–4. 6. Snyder SH. Science interminable: Blame Ben? Proc Natl Acad Sci U.S.A. 2013;110:2428–9. 7. Young NS, Ioannidis JP, Al-Ubaydli O. Why current publication practices may distort science. PLoS Med. 2008;5:e201. 8. Shanks N, Greek R, Greek J. Are animal models predictive for humans? Philos. Ethics Humanit Med. 2009;4:2. 9. Wall RJ, Shani M. Are animal models as good as we think? Theriogenology. 2008;69:2–9. 10. Greek R, Menache A. Systematic Reviews of Animal Models: Methodology versus Epistemology. Int J Med Sci. 2013;10:206–21. 11. van der Worp HB, Howells DW, Sena ES, et al. Can animal models of disease reliably inform human studies? PLoS Med. 2010;7:e1000245. 12. Roberts I, Shakur H, Coats T, et al. The CRASH-2 trial: a randomised controlled trial and economic evaluation of the effects of tranexamic acid on death, vascular occlusive events and transfusion requirement in bleeding trauma patients. Health Technol Assess. 2013; 17:1–79. 13. Pound P, Ebrahim S, Sandercock P, Bracken MB, Roberts I. Where is the evidence that animal research benefits humans? BMJ. 2004;328:514–7. 14. Mestas J, Hughes CCW. Of mice and not men: differences between mouse and human immunology. J Immunol. 2013;172:2731–8. 15. Davis MM. A prescription for human immunology. Immunity. 2008;29:835–8. 16. The trouble with animal models]. The Scientist 2007. 17. Whiteside GT, Adedoyin A, Leventhal L. Predictive validity of animal pain models? A comparison of the pharmacokinetic-pharmacodynamic relationship for pain drugs in rats and humans. Neuropharmacology. 2008;54:767–75. 18. Gould TD, Einat H. Animal models of bipolar disorder and mood stabilizer efficacy: a critical need for improvement. Neurosci Biobehav Rev. 2007;31:825–31. 19. Dzirasa K, Covington HE III. Increasing the validity of experimental models for depression. Ann N Y Acad Sci. 2012;1265:36–45. 20. Getz GS, Reardon CA. Animal models of atherosclerosis. Arterioscler Thromb Vasc Biol. 2012;32:1104–15.

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21. Suntharalingam G, Perry MR, Ward S, et al. Cytokine storm in a phase 1 trial of the anti-CD28 monoclonal antibody TGN1412. N Engl J Med. 2006;355:1018–28. 22. Marshall JC, Deitch E, Moldawer LL, et al. Preclinical models of shock and sepsis: what can they tell us? Shock. 2005;24:1–6. 23. Landis SC, Amara SG, Asadullah K, et al. A call for transparent reporting to optimize the predictive value of preclinical research. Nature. 2012;490: 187–191.

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24. Of mice and men - are mice relevant models for human disease? Outcomes of the European Commission workshop ‘Are mice relevant models for human disease’ 2010. 25. Ioannidis JPA. Evolution and translation of resarch findings: from bench to where? PLoS Clinical Trials 20060001-0005. 26. Contopoulos-Ioannidis DG, Ntzani E, Ioannidis JP. Translation of highly promising basic science research into clinical applications. Am J Med. 2003;114:477–84.

Mouse medicine and human biology.

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