WHO has released 2010 Research Agenda for Radiofrequency Fields (http://whqlibdoc.who.int/publications/2010/9789241599948_eng.pdf). It is new but, to my great disappointment, there is nothing new.
The opinion, as expected is very much influenced by the ICNIRP. Out of the 19 experts who met on February 2010 to formulate the new agenda, 10 are ICNIRP members (Main, Commission, Standing Committees, and Consulting Experts). Furthermore, the final document was edited by two ICNIRP Main Commission members, who also are (chair and member) of the ICNIRP Standing Committee – 2 Biology. Therefore, it is not a great surprise that the opinions expressed in the WHO document are going hand-in-hand with the opinions expressed by ICNIRP. Is it a good or is it a bad thing? I guess that a bit of both. Good is that, of course, all of the ICNIRP experts are well recognized scientists in this area of research. Bad is because it shows stagnation – the same scientists propagate the same scientific ideas. So there is no surprise that the agenda is lacking new ideas that could make a difference and push the research ahead. The Agenda, in my opinion lacks the vision to push science ahead.
There is focus on prospective cohort studies, what is a good thing, because it will help to avoid “disaster” of INTERPHONE. As high priority are listed prospective cohort studies in children and adolescents. This is much needed research. There are currently ongoing only case-control studies on brain tumor in children (CEFALO and MOBI-KIDS). Due to limitations of case-control study design one might be wondering if these studies will be as non-informative as INTERPHONE.
At the same time, the Agenda is “forgetting” that the prospective cohort studies are also needed for adults. There is ongoing one prospective cohort study – COSMOS – but this single study will not be enough. One could wish that a similar study would be done outside of the Europe.
Another high priority item for epidemiology is to monitor brain tumor incidence trends. This is an easy and a non-expensive way to find out whether there is any increase in brain cancer incidence within the population of mobile phone users. However, we need to remember that the focus of research on brain cancer is only arbitrary. There was no scientific basis for such research when it begun. It was just a simple assumption that if we put radiation emitting device next to our brain then the most disastrous thing that can happen is a brain cancer. This is reason why cancer was followed closely for years and reason why the majority of published studies look at cancer. However, we need also to remember that we might be “barking under the wrong tree”. That is why the COSMOS-like studies are important, because they are designed to look not only for cancer but also for other diseases and for some “non-lethal” ailments (headaches or sleep disorders). These “non-lethal” ailments are not a trivial thing because, if proven to exist, they might significantly affect our quality of life and work productivity.
Surprising in the Agenda is the continuous push for further case-control studies (neurological disorders). I think that the INTERPHONE “disaster” should be sufficient deterrent. There is no reason to waste money on new, likely non-informative, case-control studies. Effects of mobile phone radiation, if any, will be small and case-control studies will certainly not detect them reliably enough to make any valid conclusions. Neurological disorders should be included in the prospective cohort studies.
The focus here is on provocation studies examining mobile phone radiation effects on children, on brain function and on sleep EEG. Such studies are of course needed. Especially important are studies on sleep EEG where the effects, of yet unknown physiological significance, have been observed in several laboratories.
What is missing in the Agenda is the research examining whether human body responds to mobile phone radiation. We still do not know whether it is the case but, at the same time, and without this knowledge, we are debating whether this radiation could be harmful to our health.
To achieve this, we need studies that would examine effects of mobile phone radiation in humans on molecular level. We need to examine changes in gene and protein expression in easily obtainable cells (e.g. skin, blood, mucosal smears). We also need studies that would examine chemical composition of easily collectable body fluids (blood, urine, saliva). Such studies are needed to prove whether human body reacts to mobile phone radiation. There will be no physiological (or pathological) changes in our brain or other organs if there are no changes on molecular level. At the same time, when we still do not know what effects radiation could have, screening studies using transcriptomics (gene expression) and/or proteomics (protein expression and activity) and/or screening the composition of body fluids could provide us with new hypotheses and end-points for further studies.
In fact it is amazing that at the time when the biomedical science is very much based on use of transcriptomics and proteomics, the mobile telephony research is “stuck in backwaters” and seems to be avoiding these powerful technologies as much as possible. In fact, when I was pushing for this kind of research I was told that it is not good to do such studies. Why? It was explained on several occasions to me as follows:
…using high-throughput techniques of transcriptomics and proteomics scientists will always find some genes or proteins that respond to mobile phone radiation… small changes in gene or protein expression do not say yet whether there can, or can not, be an effect on our health… however, news media might write “scary” stories based on the published names of affected genes or proteins and this can have impact on the behavior of mobile phone users (e.g. decline in business)…
So, the “conclusion” was that it is better not to do such studies.
In the 2010 Research Agenda the same story seems to repeat: WHO seems to be afraid of proteomics & transcriptomics studies in humans an in vitro (see below). This WHO approach is harmful to researchers who would be interested to pursue such high-throughput screening-based research. Because WHO is not interested in it, also funding agencies hesitate to provide grants.
What else is, in my opinion, missing from the human studies in the new Research Agenda:
- Studies looking for sensitive subpopulations – here I am not referring to the so called, and self-diagnosed, electromagnetic hyper-sensitivity (EHS) or new term for this phenomenon: idiopathic environmental intolerance (IEI). I am referring to a phenomenon of individual sensitivity, where different people, due to the different genetical background, react differently to the same stimulus – might be more sensitive than the majority of population.
- Studies looking at human fertility – animal and in vitro research suggests that there might be effects.
- Studies looking at possible effects on blood-brain barrier – animal and in vitro research suggests that there might be effects.
There are two high-priority research needs. One is to look at developmental and behavioral changes in animals exposed in womb and soon after birth. Yes, such studies are not possible to perform in humans for ethical reasons. On the other hand is necessary to remember that if we see effects then we need to be cautious because there might be risk for humans. However, if we do not see effects it does not automatically mean that there are no effects in humans. Animals are not humans.
The other priority is to look at neurodegenerative effects. This is also good to study in animal models. However, surprisingly, the authors of the Research Agenda refer here to the recent study of Arendash et al. (http://iospress.metapress.com/content/v37225v0067x3430/) that concluded that mobile phone exposures can prevent (Agenda writers used term “affect” even if the study authors spoke about prevention) development of Alzheimer disease in genetically modified mice. Use of this reference is surprising. Throughout the Research Agenda text the authors are stressing how important is good study design and good dosimetry and then they use as a valid reference a study that had so poor dosimetry (non existent; see photo of exposure set-up on BBC news: http://news.bbc.co.uk/2/hi/8443541.stm) that based on it is not possible to draw any conclusions about the causality of the effect.
As less important research need is listed effect of mobile phone radiation on reproductive organs. Why it is less important than embryonic development or neurodegenerative diseases?
In general, I would hesitate, right now, to list animal studies within the high priority area and advise to perform new studies. There is ongoing a large animal study by the US National Toxicology Program. In current situation of the lack of knowledge whether this radiation affects humans, instead of new animal studies I would rather focus on human molecular-level studies where real people are exposed to radiation, at levels permitted by the current safety standards. It is ethically permissible. Only after we determine that human body indeed responds to this radiation, more animal studies will be justified. So, let’s not kill unnecessarily animals for not justified studies.
In this research area there are not listed any high-priority studies to perform. Therefore the discussion whether radiation affects:
- cellular stress response pathways that, among others, may regulate carcinogenicity,
- causes DNA damage,
- cell responses in transcriptome- or proteome-dependent manner,
will remain unanswered.
As non high-priority (other) research needs is listed search for optimal cell types and techniques to study effects of this radiation. Not all experimental methods are sufficiently replicable or not all cells seem to be responding to this radiation. So, finding the best methods and cells might help to obtain more robust results.
The high-throughput techniques are mentioned here but are not listed as any kind of “priority”. There is an agreement that studies using them should help identify target molecules of the radiation. Also, the authors of the Agenda agree that the studies should be of good quality. This is not always the case with the few published studies. The authors of the Agenda also stated that the so far observed effects on genes and proteins are small and difficult to interpret. Finally, the Research Agenda concludes “…The use of these high-throughput techniques in exploring possible RF EMF effects may become a priority once these issues have been addressed.”.
The so far published studies that used high-throughput screening techniques should be, in my opinion, considered as “pilot studies”, pawing the way for further, better designed (area develops very rapidly and techniques improve very fast), studies. The major obstacles are the “negative attitude” towards such research and, in part caused by it, lack of funding. Without sufficient funds researchers need to “cut corners” and the study design or execution will suffer. Then, the argument of not well designed/executed studies is used by the Research Agenda authors to perpetuate the problem. As long as the high-throughput studies will not be considered as the high-priority research that long it will not be possible to receive sufficient funding and the problem of lesser quality studies will perpetuate.
Why it is so that transcriptomics and proteomics are considered to be excellent research tools in any area of biomedical research. But they are considered “taboo” in research of electromagnetic fields effects on humans? Is someone afraid that by using them we might find some significant effects on human physiology?
We see biological effects of this radiation and we do not know the mechanism – but the Research Agenda does not see any research need in this area. Why?
Studies on signal transduction (e.g. stress response kinases and stress response proteins) and studies on radiation distribution within the cell (see my earlier blog on thermal effects) are needed to find out how the observed effects are caused. This last issue connects mechanisms with the next area of research:
There has been great progress in human dosimetry. Variety of dosimetry models for humans of various age, shape, size and geographical origin have been developed. Also models for the exposure of children in the womb are being developed. This area of research seems to thrive, as compared with biological effects research.
However, one area of dosimetry, that is much needed to help to determine the mechanisms of the effects – the micro-dosimetry does not progress. In 2006 Research Agenda it was listed as research that is needed but there has been no research done. Was it not sufficiently highly prioritized?
Social science research needs
This is the last area of research needs considered in the research Agenda. It does not prioritize research needs. It suggests research on how people perceive the research on mobile phones, the precautionary advice, and the rapid changes in the technology. It is indeed important to develop good communication methods between scientists, public health officials and general public in order to avoid misunderstandings. The problems should not be blown-out-of-proportion but also understating should be avoided in the situation of current scientific uncertainty.
There is nothing new in the research agenda proposed in 2010. There is no vision how to push the research ahead and resolve the existing controversies. In fact many of the existing controversies were “forgotten” in the Agenda. There is no vision how to modify research approach to get the much needed answers. This indicates, in one word, stagnation. It is discouraging that the experts, considered as being among the best in the field, did not prepare better advice for how to continue research and what to change, so that the better and more reliable scientific studies will be produced.
Especially disappointing is the lack of advice/suggestion of what novel research technologies could be used to clarify the old contradictory results. The agenda seems to focus on very limited (too limited) number of research topics but it forgets that the new research approaches and new research technologies are needed to bring closure to the issue of mobile telephony and health. Without the push for new approaches the same topics will be examined again and again with the same methods without bringing resolve.