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Blood Transfus. 2017 March; 15(2): 104–106.
PMCID: PMC5336329

Large retrospective effects, clear differences in animals, and multiple negative randomised controlled trials: this is exactly how it is supposed to work

A series of randomised controlled trials (RCTs) have recently been completed regarding the clinical relevance, or lack thereof, of the “age of blood” in red blood cell (RBC) transfusion15. The results of the most recently completed study, the INFORM trial (“Informing Fresh versus Old Red cell Management”), were presented during the Plenary Session of the 2016 American Association of Blood Banks (AABB) meeting, and the paper is now available in the New England Journal of Medicine3. To date, none of these RCTs have detected any significant differences in the medical outcomes measured following transfusion of fresh RBCs vs standard issue (i.e. “older”) RBCs. Although no study has purposefully transfused the oldest possible RBCs (i.e. 42 days) to any patient population, analyses of those who did receive the oldest units by chance likewise failed to detect any significant differences in any evaluated clinical outcome, although, the latter analyses did not have a great deal of statistical power. These results have led to some concern regarding the discrepancy between the new results with RCTs and prior results from observational studies in human patients and prospective studies with healthy human volunteers and animal models. For example, why did the study by Koch et al.6, and many other studies, observe increased morbidity and mortality associated with transfusions of longer-stored RBC units? In addition, why has so much animal model data in multiple species (mice, guinea pigs, dogs, sheep, etc.) similarly observed multiple adverse outcomes, by multiple pathophysiological mechanisms, following transfusions of longer-stored RBCs? Such a clear failure of outcomes must reflect some fundamental error; in short, where did so many of us go so wrong to mislead the field and waste significant resources on misguided science?

This question, while seemingly complex, is actually very easy to answer; that is, nothing went wrong. Indeed, this is exactly how scientific inquiry is supposed to work. Thus, although RCTs remain our best tool to mitigate bias in observing natural phenomena in human populations (in accordance with methodological constraints consistent with our ethical values), RCTs are resource intensive efforts. Therefore, it is not cost effective to perform RCTs as a first-line approach to observing clinical events, adverse or otherwise, especially those that occur at a low frequency. Rather, retrospective and observational studies, driven by analysis of captured data, or even inspired by anecdotal observations, remain our most powerful surveillance method for phenomena that would otherwise go undetected. Indeed, the history of medicine is rife with such examples, encompassing successful ones (e.g. digitalis, smallpox vaccination, artemisinin) as well as many failures. Such critical analysis is ongoing in essentially all fields by our front-line observers; for example, were it not for real-time observational reports, then the association between Zika virus infection and microcephaly would not have been detected. Not to perform such studies and publish such observations would be, in our view, an abdication of our responsibility to monitor and assess human (patho) biology and medicine. It is exactly because such studies can result in type I errors, due to the unavoidable bias intrinsic to such methods, or due to just chance alone, that it is wise and appropriate that resources then be expended on subsequent RCTs, when justified by the size and/or implications of the detected effects. However, the failure of subsequent RCTs to observe the phenomena detected by the antecedent retrospective studies does not demonstrate that the retrospective approach is wasteful. Rather, as vanguards of what human diseases or sequelae that we can detect, a substantial false determination rate is an expected and inevitable quality of approaches with sufficient sensitivity to allow detection of important medical issues. In addition, RCTs will not detect (nor can they confirm or refute) very low frequency occurrences, due to the practical limit on statistical power that RCTs carry as a function of the costs required for their performance. Indeed, the suspicion that longer-stored RBCs may produce adverse effects is reasonable based upon general notions of metabolic ageing, in vitro analysis of stored human RBCs (i.e. the RBC “storage lesion”), and animal models that demonstrate such sequelae, in general, and also in specific settings. Thus, we would have been remiss as a field not to study this issue and address this question in the most rigorous way possible. That the recent RCTs showed no detectable differences at the limits of their statistical power provides great comfort that the general standard of care will not be improved by issuing fresh blood, at least for the clinical indications that were studied.

Of course, we cannot rule out very small effects that may be detected by large retrospective or observational studies, but for which RCTs cannot be powered in any practical way. However, if we accept that science consists of a body of knowledge, the final adjudicator of which is observation of the natural world, and if we accept that our observations are limited by the resources available, then there is no practical difference between phenomena that we cannot observe and those that do not exist (“For whereof we cannot speak, thereof we must be silent”)7. Still, when approximately 80 million RBC units are transfused annually worldwide, even vanishingly small events, if they are real, can affect actual human lives; it then becomes a question of ethics and economics whether it is “worthwhile” to study and attempt to prevent them.

What are we then to make of all the animal data generated in modelling a human effect that may not even exist? How many resources were “wasted” on such investigations and how many animals were needlessly subjected to “meaningless” studies? The key redeeming fact about such studies is a counterintuitive utility even to that which does not translate. If transfusions of longer stored RBCs have no clinically-important effects in humans, then studies of their effects in animals cannot translate to the human setting. Accordingly, what is the meaning of modelling something that does not exist? At first consideration, it seems that this notion is not possible; if the phenomenon being “modelled” does not exist, then is one modelling anything at all? Of course, the answer is “yes”, just because scientists may not know what they are modelling does not mean they are not modelling something useful.

In one of the best descriptions of how research really works, Peter Medawar, the immunologist and Nobel laureate, detailed how experiments in tumour transplantation in mice examined a biology that does not occur in humans8. However, far from modelling nothing, they were inadvertently modelling tissue transplantation, and, eventually, the biology of histocompatibility and immune recognition, in general. When Bruce Beutler, another immunologist and Nobel laureate, and his colleagues became interested in the effects of endotoxin in mice, it was already well understood that “septic mice” have a drop in temperature instead of a fever, which seems to be a poor model for human biology. Even worse, Dr. Beutler focused on the very few mouse strains in which endotoxin had no effect; this was clearly the single worst model for sepsis! However, it was precisely this “broken” response that allowed him to identify a specific toll-like receptor as the murine, and then human, response element to endotoxin9. Like Medawar’s description, the greatest utility of this finding was in enhancing our understanding of innate immunity in all of its manifestations.

So, now, what about all the animal data generated regarding transfusion of longer-stored RBCs and its various sequelae? Do they model effects that really occur in humans in general, but too infrequently to be observed? Or do they model effects in particular patient populations that have not yet been studied in the RCTs? Alternatively, are we modelling some other biology that we are, as yet, unaware of that is linked to the biology of longer-stored RBC transfusions? Perhaps we are modelling something unrelated to human biology at all, although this seems unlikely, given the close evolutionary relationships among mammals. Still, it remains possible that we are studying biology relevant only to our livestock, our companion animals, and the vermin in our sewers. Nevertheless, although we do not yet understand the utility of this knowledge, the history of science teaches that the effort is not wasted effort as long as the experiments are properly designed, rigorously performed, and accurately reported. The data are what the data are, but their interpretation, meaning, and importance will evolve over time in the context of our ever-expanding base of scientific knowledge.

At the cost of sounding self-congratulatory (as the authors are a small part of the modelling efforts of longer-stored RBC transfusions), it seems appropriate to congratulate the field of Transfusion Medicine and the various funding agencies for rising to the occasion and keeping an open mind regarding potential issues affecting patient care, for asking whether such effects might be present, and for acting in a rigorously scholarly and scientific fashion. The detailed investigations of humans, and the simultaneous modelling studies in vitro, in animals, and in human volunteers, have generated a new body of knowledge, the greatest utility of which is likely not yet clear. However, what is clear is that we not only kept a watchful eye on potential problems, but also did not rush impetuously into making reflexive changes, without careful scrutiny and study. The field is also indebted to the support from government, public sector, and industry sources to allow such studies to be performed. At the end of the day, we understand much more now than we did when we started, and we are more knowledgeable about what is best for our patients, and how best to save human lives, while doing the least harm. This is exactly how it is supposed to work. The lack of any detectable effect of RBC storage on clinical outcome in the published RCTs is a highly pertinent negative, and the last decade has been fruitful, even if the end point of the journey has not been what, at least some of us, anticipated at the beginning. In the words of George Harrison, paraphrasing a conversation between Alice and the Cheshire Cat10, “If you don’t know where you’re going, any road will take you there”11. What has just occurred in the field of blood storage biology is exactly how the scientific process is supposed to work.


The Authors declare no conflicts of interest.


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8. Medawar P. Can Scientific Discovery be Premeditated The Limits of Science. Oxford; Oxford University Press; 1984. pp. 46–7.
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