The Harvard Study on Neonicotinoids and CCD
A recent press release by the prestigious Harvard School of Public Health claims that one of their researchers has found that Colony Collapse Disorder was caused by a common insecticide used on corn. As an informed beekeeper and environmentalist, I feel that this study calls for standard scientific scrutiny to see whether their claims actually have merit.
At first glance, the study indeed appears to support the hypothesis that chronic exposure to field realistic doses of imidacloprid during summer and fall can lead to late winter collapse of the treated colonies. But the devil is in the details…
The study got off to a good start—several colonies were fed different “field realistic” doses of imidacloprid in syrup, and colony populations and brood area were measured. Had the authors stuck to this original design (which has already been performed numerous times in several countries) the results would have been meaningful. Indeed,after a month of feeding such syrup, the investigators did not observe any adverse effects upon the colonies due to the insecticide!
But then, since the lead investigator seemed to be eager to “prove” that CCD is caused by imidacloprid, he dreamed up the fantastic scenario that in the winter of 2006/2007 that for some inexplicable reason the nation’s supply of HFCS was contaminated with high levels of imidacloprid. My reading of the paper suggests that the author knows little about bees, little about pesticides, nothing about HFCS, had no understanding of the distribution of systemic pesticides in plants. This paper is an example of authors so bent on “proving” that imidacloprid is the cause of CCD, that they strain credulity with some of their assumptions and reasoning, and even by changing the experimental protocol midstream!
When the investigators failed to prove their case after a month of feeding spiked syrup—they changed the protocol, and ramped up the doses of insecticide in the syrup to sky high and overtly toxic levels, and then made a series of compounding mistakes, notably by not performing the sort of necessary parasite management required for colonies to survive the winter. And then, even though the symptoms of the colonies when they died did not match the symptoms of CCD, yet the Harvard press agent claimed that they did!
Unfortunately, there are also a great number of factual misrepresentations and quite a bit of fuzzy thinking in the paper, which obviously was not peer reviewed by any bee biologist nor toxicologist. I realize, in retrospect, that some of my comments may sound a bit snarky, and I apologize to the authors, whom I’m sure were earnest in their quest to prove their anti-neonic agenda. Back to the paper, allow me to discuss some of the problems. The author stated in an interview:
“When other conditions cause hive collapse—such as disease or pests—many dead bees are typically found inside and outside the affected hives.”
Could someone please refresh my memory? Other than in the case of tracheal mite, which diseases or pests leave many dead bees in a hive? (Note that starvation or acute pesticide toxicity would not fall into the category of “disease or pest”). The point is, that the natural behavior of sick or old bees is to abandon the hive—one normally does not find dead bees in hives that have died from parasites, including viruses.
Let’s look at a few more sentences from the paper:
“We hypothesized that the first occurrence of CCD in 2006/2007 resulted from the presence of imidacloprid … in high-fructose corn syrup (HFCS), fed to honey bees as an alternative to sucrose-based food. There are three facts to support this hypothesis. First, since most of the suspected but creditable causes for CCD were not new to apiculture, there must have been an additional new stressor introduced to honey bee hives contemporaneous with the first occurrence of CCD during the winter months of 2006 and early 2007.”
In fact, beekeepers who had never fed HFCS experienced plenty of cases of CCD. Plus, new stressors such as Nosema ceranae and novel strains of viruses have been strongly associated with colony mortality.
The authors give no justification for their assumption that there was any change in HFCS in 2006. And as Bob Harrison and others have pointed out, CCD actually started occurring in 2004-2005, prior to the authors’ assumption that tainted syrup hit the market beginning in 2006. Any HFCS produced from such treated corn would have necessarily have been produced following the season of harvest.
The authors then cite a few studies that show that systemic insecticides are translocated, as they are intended, throughout the plants. But then they stretch by stating:
“ These study results lend credence to our hypothesis that the systemic property of imidacloprid is capable of being translocated from treated seeds to the whole plant, including corn kernels and therefore likely into HFCS.”
My gosh, this is one helluva assumption! Without taking the time to simply confirm that imidacloprid winds up in the kernels, the authors assume that it is concentrated there at high levels! All they had to do was to look at the freely-available results of USDA annual testing of foods for pesticide residues—they would have found that of the 655 samples of corn grain tested, absolutely none showed residues of either imidacloprid or clothianidin!
And then they further go out on a limb by assuming that their imaginary residue of imidacloprid was then somehow concentrated when the corn was used to produce HFCS (ignoring the fact that the vast majority of corn is treated with clothianidin, rather than imidacloprid). As if that weren’t enough, the authors go into la-la land with some even wilder creative assumptions:
“Since there is no tolerance level for imidacloprid in HFCS, we applied a 10-fold concentrating factor, or 0.5 ppm (500 μg/kg) of imidacloprid in HFCS, by taking into account the uptake by corn plants from seeds that are treated with imidacloprid.”
They simply created this “concentrating factor” out of thin air! They give absolutely no justification for it. In the actual process of making HFCS, pesticides are largely removed. As I stated before, all that the authors had to do would have been to ask Roger Simonds at the USDA Gastonia pesticide testing lab as to the actual measured levels of imidacloprid in HFCS, and thus would not have brought embarrassment to Harvard School of Public Health by such a ludicrous assumption.
The paper turns into farce when the author states:
“we used food-grade HFCS fortified with different levels of imidacloprid, mimicking the levels that are assumed to have been present in the older HFCS.”
Why in the world would the authors “assume” that imidacloprid was present in the older HFCS, but not present in the HFCS that he used in the current study to feed the control colonies? But then they go on to state:
“ The range of dosages used in this study from 20 to 400 μg/kg were not only environmentally relevant…”
Since when has 400 ppb ever been been considered to be “environmentally relevant”? Levels of 1-4 ppb are environmentally relevant; levels above 40 ppb are usually considered to be overtly toxic. So the 400 ppb level is 100 – 400 times as strong as the normal measured levels in the field due to seed treatment!
“Therefore, we are confident that the imidacloprid dosages applied in this study would be comparable, if not lower to those encountered by honey bees inside and outside of their hives.”
Unfortunately, the authors’ confidence is not supported by any actual field measurements by numerous other researchers across the world!
The authors state: “There are several questions that remain unanswered as a result of this study. First, the systematic loss of sealed brood in the imidacloprid-treated and control hives may indicate a common stress factor that was present across all 4 apiaries.”
Like, maybe the feeding of 71 (yes, seventy-one) pounds of HFCS was not the best nutrition for the colonies! The authors neither gave the source of their corn syrup, nor whether it was a brand that has been tested by beekeepers as suitable feed (some brands cause bee health issues). Since all the colonies in the trial (test and control) started going downhill (and since a quarter of the control colonies also died), it is difficult not to ignore that something was seriously wrong with the entire experimental design!
More to the point, the field investigators should have taken a few nosema or varroa counts, rather than simply assuming that these common parasites weren’t killing the colonies! For all we know, all the hives could have beeb crawling with varroa or badly infected with nosema. One statement suggests that varroa was evident: “nor a large number of Varroa mites was observed in hives during the summer and fall seasons,” which suggests to me that the investigators are admitting that mites were indeed observed!
Let’s look at varroa: the study states that 3-lb packages were installed on March 28. Surprisingly, “By May 21st, 2010 all twenty frames in each of 20 hives were drawn out into comb and contained at least 14 frames of capped brood.” These colonies really took off, meaning that they were virtual varroa breeding grounds. By late July they averaged about 25,000 cells of sealed brood.
Strange and Calderone (2009) found Eastern package bees to contain about 3 mites per hundred bees, which would work out to about 300 mites in a 3-lb package. When colonies are rapidly expanding, mite populations double each month. So from late March through late July, we’d expect the mite populations in these hives to reach 4,800 by late July. This is a very serious mite infestation level! Yet, the researchers waited until October 5 to treat with Apistan strips (which are ineffective against mites in many areas of the U.S.)! Any experienced beekeeper would suggest that these colonies died from a varroa/Deformed Wing Virus epidemic, which leaves deadouts, as the authors observed, “remarkably empty except for stores of food and some pollen left on the frames.” Unfortunately, the authors only included a photo of a honey frame, rather than a brood frame, which might have been helpful in diagnosing the actual cause of death! The dosing with high levels of an insecticide would be expected to cause the treated colonies to suffer more from varroa than the untreated controls.
The description of the dead colonies does not match the definitive signs of CCD at all—there was a dwindling of population, rather than a sudden collapse, and no abandoned brood. Rather the descriptions of the deadouts more closely matched dwindling collapse due to varroa/virus or nosema.
The authors, on a roll, simply do not know when to stop: “If imidacloprid exposure is truly the sole cause of CCD, it might also explain the scenario in which CCD occurred in honey bee hives not fed with HFCS. Considering the sensitivity of honey bees to imidacloprid as demonstrated in this study and the widespread uses of imidacloprid and other neonicotinoid insecticides, pollen, nectar, and guttation drops produced from those plants would have contained sufficient amounts of neonicotinoid insecticide residues to induce CCD.”
What are they talking about when they say “considering the sensitivity“? Even the lowest fed dosage (20 ppb) is about 5-20 times higher than that commonly found in nectar, and the other three doses were far higher–it is amazing to me that the colonies were not killed outright!
Speaking of which, I find it odd that the investigators didn’t give any explanation as to why they changed treatment dosages mid trial. To their credit, they initially treated the colonies with “field realistic” doses of the insecticide: 0.1 – 10 ppb. I suspect that after feeding the colonies for four straight weeks in July, and not noticing any adverse effects, that they then decided that they had better really hit the colonies hard if they wanted to “prove their case”–so they arbitrarily ramped up the lowest dose to 200 times stronger, and the highest dose to 40x stronger (that oughtta do it!).
When I do the math on their insecticide spiking, their three higher doses provided enough imidacloprid to theoretically kill every single bee in every hive! I find it hard to understand how they can claim that the dosages were anywhere near “field relevant.”
I can only imagine their surprise and disappointment when after nine weekly feedings of a full half gallon of syrup intentionally spiked to overtly toxic levels, that they still noted virtually no adverse effects! Surprisingly, the amount of broodrearing was unaffected at the 20, 40, and 200 ppb dosages, and only slightly depressed at the clearly toxic 400 ppb dose! Note that all the colonies were still alive at midwinter, fully 3 months after the dosing ended! If anything, this study clearly demonstrated that colonies of bees can survive prolonged poisoning by imidacloprid at excessively high levels!
So why did the colonies die? Such insecticide exposure to hives in late summer has been previously demonstrated to greatly increase the chance of a colony later dying from nosema or varroa infection during the winter. In this study, poisoning the colonies all through late summer and early fall likely hampered the ability of the colonies to prepare a healthy population for winter.
The investigators state that they also took biweekly measurements of the cluster sizes of the colonies, yet oddly chose not to include the results in the paper. This makes me wonder whether the authors simply decided to exclude any data that did not support their hypothesis?
So although this paper is surely going to be cited by anti-neonic advocates as some sort of supportive evidence, I find it to be a case in which an initially well-designed study (the dosing of hives with a series of four field realistic doses of imidacloprid) turned to farce when the investigators arbitrarily ramped up the doses, and blew it on parasite management.
In my assessment, it appears that the data from this study actually support an alternative hypothesis–that field realistic doses of imidacloprid had no measurable adverse effects upon the colonies. And even patently toxic doses had little immediate effect. I suspect that the apparent delayed effect was due to the impact of the insecticide upon late summer colony populations (which the authors inexplicably did not present), which led to later collapse due to parasite buildup.
In reality, the neonicotinoids fully appear to be “reduced risk” insecticides, which under field conditions, when properly applied (no dust issues) have never been associated with significant colony health issues. Compared to alternative insecticides, the data to date (including that of this study) support the hypothesis that neonicotinoid, when used as seed treatments, are an improvement over the previous classes of insecticides (there are clearly some questions about dust issues, chemigation, foliar and landscape treatments, which I will discuss in an upcoming article).
I find it unfortunate that the press, including both of our national bee journals, gave publicity to this paper without any sort of critical analysis. Such messages only confuse the public. Pesticides are a major issue to the beekeeping community. What we need are well designed and executed studies, (as well as better enforcement of pesticide law) in order to solve these problems. Sadly, this study just confuses the issues.
UPDATE JUNE 13
I am occasionally asked to referee scientific publications. So I contacted the authors of the paper, and asked them if they would answer the sort of questions that I would have asked about their manuscript had I been asked to review the paper prior to publication.
I also sent the questions to the editor of the Bulletin of Insectology in order that they could be published for scientific debate in the usual manner in the Letters page, but unfortunately his publication is not set up for that type of discussion.
Unfortunately, after seeing the questions, the authors chose not to defend their work, so the questions in the abbreviated list below remain unanswered.
[I have also added a few comments italicized in brackets]
Readers will likely wish to have a copy of the study  at hand. It can be freely downloaded athttp://www.bulletinofinsectology.org/pdfarticles/vol65-2012-099-106lu.pdf. Remember, these are the typical sort of questions that a peer reviewer would ask when a manuscript is submitted for publication—the referee is expected to go over the paper detail by detail, check the math, make sure that previous research is cited, a challenge the author’s interpretation of the data.
The authors’ experience
Q: Could you perhaps briefly state for the benefit of my readers, your experience as apiarists?
Your assumptions and background research
vanEngelsdorp (2009) reported that “Large-scale losses are not new to the beekeeping industry; since 1869, there have been at least 18 discrete episodes of unusually high colony mortality documented internationally. In some cases, the descriptions of colony losses were similar to those described above.”
In my own beekeeping career, losses due to the initial tracheal mite invasion often reached 70%, and for varroa, up to 90%. Wilson (1979) reported losses in the ‘70s to “Dwindling Disease” that were nearly as extensive as those from CCD (and the reporting at the time was not fueled by media coverage). His maps of DD distribution were nearly identical with those of the 2006/2007 CCD incidence.
Q: Could you please provide supportive evidence to substantiate your claim that: “never in the history of the beekeeping industry has the loss of honey bee hives occurred in such magnitude and over such a widely distributed geographic area”
[In the following paper, Wilson had a map of the widespread problem of "Disappearing Disease" in 1979. Wilson, WT and DM Menapace (1979) Disappearing Disease of Honey Bees: A Survey of the United States. ABJ March 1979: 184-217.]
You state: “First, since most of the suspected but creditable causes for CCD were not new to apiculture, there must have been an additional new stressor introduced to honey bee hives contemporaneous with the first occurrence of CCD during the winter months of 2006 and early 2007.”
Q: Could you please explain why do you not consider the recent invasion of Nosema ceranae, the novel ubiquitous presence of DWV, nor the apparent recent invasion of IAPV to be novel “stressors?
A very similar trial was performed by Faucon (2005), with substantially different results. As you are well aware, it is standard practice in scientific papers to cite previous similar research. Yet you do not cite Faucon, nor any other studies in which spiked syrup or pollen was fed to colonies in situ. [It is a scientific obligation for any author to cite previous research on the subject when he publishes a paper].
Q: Why did you not cite and discuss previous research, especially that in which the findings conflicted with yours?
Justification of the imidacloprid in HFCS hypothesis
The central tenet of your paper is your hypothesis that HFCS (high fructose corn syrup) in 2006 was tainted with residues of imidacloprid: “The widespread planting of genetically engineered corn seeds treated with elevated levels of neonicotinoid insecticides, such as imidacloprid since 2004 (Van Duyn, 2004), and their acute toxicity to honey bees led us hypothesize a link between CCD and feeding of HFCS containing neonicotinoid insecticides.”
In response, Bayer Crop Science claims that imidacloprid has never been used on more than about ½ of 1% of corn plantings in the U.S.
Q: Do you have evidence to the contrary, or evidence to suggest that the harvest of that 0.5% of corn seed would have been preferentially used to produce HFCS?
You state: “it was the timing of the introduction of neonicotinoid insecticides to the cornseed treatment program first occurring in 2004/2005 that coincides with CCD emergence”
Dr. Eric Mussen observes that several California beekeepers (including myself) experienced CCD in our operations beginning as early as the fall of 2004. This does not appear to fit with your introduction of seed treatment timing. Nor did Dr. Bromenshenk’s CCD survey find any correlation between CCD and the feeding of HFCS.
Q: Do you have supportive evidence that apiaries fed HFCS were more at risk for CCD?
A major problem with your study, in the minds of many, is the lack of support for your core hypothesis that imidacloprid contamination of corn syrup indeed actually occurs.
Q: Your hypothesis is that CCD was caused by residues of imidacloprid in HFCS fed by beekeepers to their bees. Since CCD still occurs through the current time, it seems then that you should be able to find it in 2012 syrup. Yet in your own testing, there was no trace of imidacloprid in your samples of HFCS. Some reviewers feel that your own testing disproved your hypothesis!
Q: Could you please give an explanation for this inconsistency?
Q: Could you please explain your reasoning as to what had changed in the process of HFCS manufacturing between 2007 and the time that you purchased your HFCS (2010?) that would have caused pesticide residues to disappear?
One would assume due diligence on your part to check to see whether the commercial corn seed from which HFCS is manufactured actually contained residues of imidacloprid. As an “ad hoc panel member of the US EPA Federal Insecticide, Fungicide, and Rodenticide Act (FIFRA) Scientific Advisory Panel,” your lead author (Dr. Lu) would certainly be aware that any residues of pesticides in corn grain would have been published in the USDA’s readily available “Pesticide Data Program Annual Summary, Calendar Year 2007” .
In Appendix F of that document (Distribution of Residues by Pesticide in Corn Grain), one can easily find that in 2007 the USDA tested 655 samples of corn grain (from which HFCS is made) and found absolutely no detections whatsoever of either imidacloprid or clothianidin! Is seems odd to base your entire study on a hypothesis which the main author had every reason to know was unsupported by simple facts!
Q: Could you please explain why you did not mention the absence of residues in corn seed in USDA testing?
You state: “It should be noted here that the residue levels of imidacloprid, or other neonicotinoid insecticides, have not been routinely monitored in HFCS.” You call for us to note this as a fact.
Q: Do you have documentation HFCS is not tested by the USDA or the HFCS manufacturers?
A simple internet search  reveals that the ARS Tucson Bee Lab tested HFCS for both bee toxicity and contaminants in 2008.
Q: Why do you not mention this, nor cite their results in your paper?
You state: “One apparent deficiency, in addition to the small number of honey bee hives used in this study, is that we were not able to obtain HFCS manufactured in 2005/2006 for use in this experiment.”
Q: In light of the fact that the HFCS manufacturers are livid over your accusation that their product was contaminated by a pesticide, implying that they threatened the U.S. populace with pesticide exposure in common food products, did you actually ask the manufacturers to supply archived samples for testing?
Q: And if not, have you yet done so?
Perhaps the most controversial aspect of your study is the statement: “Since there is no tolerance level for imidacloprid in HFCS, we applied a 10-fold concentrating factor, or 0.5 ppm (500 μg/kg) of imidacloprid in HFCS, by taking into account the uptake by corn plants from seeds that are treated with imidacloprid.”
This is a pretty strong assumption, and implies that the EPA, the USDA, the FDA, and the corn syrup manufacturers were all derelict in their duty to protect the public from exposure to high levels of an insecticide in a ubiquitously-used sweetener in the American diet!
Frankly, it appears that your 10-fold “concentrating factor” was simply dreamed up!
Q: What supporting evidence do you have that would suggest that the insecticide would be concentrated by a factor of 10 (as opposed to being removed) in the manufacturing process of HFCS from corn kernels?
Justification of the claim of “field relevance” of dosages
You state: “The range of dosages used in this study from 20 to 400 μg/kg were not only environmentally relevant to those reported imidacloprid levels by studies that are cited previous…”
In a recent review, Cresswell (2011, whom you also oddly do not cite in your references) suggests that “the field-realistic range of imidacloprid concentrations is assumed to be 0.7–10 μg L-1.” [forbenefit of the reader, μg/kg is equivalent to ppb (parts per billion); μg L-1 is similar, but by volume, rather than weight].
I commend you on your initial range of doses (0.1, 1, 5, and 10 ppb), which do indeed reflect typical levels found in nectar, with 10 ppb being at the far high end.
But after four weeks of feeding these field realistic doses, without explanation in the paper, you switched to much higher concentrations of the insecticide (20, 40, 200, and 400 ppb)—levels which would be considered to be overtly toxic to honey bees! This is a key question, and a major criticism of the study.
Q: Could you please elaborate as to why you changed the dosages mid study, and why you apparently changed your minds as to what constituted “environmentally relevant” levels.
In an excellent recent review on the ecotoxicity of neonicotinoid insecticides to bees (which you also inexplicably failed to cite), Decourtye and Devillers (2010) note that “acute exposure [100 ppb] cannot probably occur in the realistic conditions since the concentrations of imidacloprid and its metabolites, to which honey bees are exposed always have been measured lower than 10 [ppb].”
Q: Could you please explain how you arrived at the range of high doses that you used, since they appear to be far above (up to 40 times higher than) field-realistic doses?
Q: Could you please specifically cite studies that have found 400 ppm of imidacloprid in nectar to which bees would normally be exposed to the extent that it could be associated with widespread CCD?
You state: “Considering that honey bees were diluting the concentrations of imidacloprid fed to the hives with natural nectars foraged during the HFCS feeding months (July to September)…” Yet earlier in the same paper you state that the colonies experienced a nectar dirth [sic] during this period of time. These two statements appear to be contradictory!
Q: Do you have any daily weight gain data to support your contention that the treated syrup was indeed diluted by nectar during the feeding period?
You state: “Therefore, we are confident that the imidacloprid dosages applied in this study would be comparable, if not lower to those encountered by honey bees inside and outside of their hives.”
I find it difficult to believe, by any stretch of the imagination, that nine weekly feedings of half gallons of 67% sugar solution (for a total of 51 pounds per colony) spiked at 400 ppb (or even 20 ppb) imidacloprid, during the nectar dearth, could be construed to mimic any field-realistic exposure of colonies to the insecticide!
Q: Would you care to comment?
Questions on parasite monitoring and management
You state that: “Hives were monitored weekly, and managed using standard beekeeping techniques.”
As I’m sure you know, there are few observable signs for varroa infestation, and there are no field signs of Nosema ceranae infection. Standard beekeeping management these days involves the monitoring of varroa mite levels, typically by natural mite fall, either roll, or alcohol wash .
[Since all the colonies in the trial (test and control) started going downhill (and since a quarter of the control colonies also died), it is difficult not to ignore that something was seriously wrong with the entire experimental design!
More to the point, the field investigators should have taken a few nosema or varroa counts, rather than simply assuming that these common parasites weren't killing the colonies! For all we know, all the hives could have been crawling with varroa or badly infected with nosema. One statement suggests that varroa was evident: "nor a large number of Varroa mites was observed in hives during the summer and fall seasons," which suggests to me that the investigators are admitting that mites were indeed observed!
Let’s look at varroa: the study states that 3-lb packages were installed on March 28. Surprisingly, “By May 21st, 2010 all twenty frames in each of 20 hives were drawn out into comb and contained at least 14 frames of capped brood.” These colonies really took off, meaning that they were virtual varroa breeding factories. By late July they averaged about 25,000 cells of sealed brood.
Strange and Calderone (2009) found Eastern package bees to contain about 3 mites per hundred bees, which would work out to about 300 mites in a 3-lb package. When colonies are rapidly expanding, mite populations double each month. So from late March through late July, we’d expect the mite populations in these hives to reach 4,800 by late July. This is a very serious mite infestation level! Yet, the researchers waited until October 5 to treat with Apistan strips (which are ineffective against mites in many areas of the U.S.)! Any experienced beekeeper would suspect that these colonies died from a varroa/Deformed Wing Virus epidemic, which leaves deadouts, as the authors observed, “remarkably empty except for stores of food and some pollen left on the frames.” Unfortunately, the authors only included a photo of a honey frame, rather than a brood frame, which might have been helpful in diagnosing the actual cause of death! Note also that the dosing with high levels of an insecticide would be expected to cause the treated colonies to suffer more from varroa than the untreated controls.]
Q: Did you monitor mite levels during the trial? If so, could you please elaborate on your testing method and share the results?
Nosema is a common pathogen, currently infecting about 50% of colonies, and can be deadly to colonies during winters such as yours.
Q: Did you take any samples of bees from the colonies to monitor for nosema levels? If so, could you please share the results?
You state: “Since all hives were considered healthy as they went into fall season, those pathogens posed very little threat to the health of honey bee hives.”
Q: Could you please elaborate on how you determined that the colonies (hives are the wooden boxes) “were considered healthy,” especially in light of the “systematic loss of sealed brood” that you report in your Discussion?
I am surprised that the investigators waited until October 5 to treat for varroa. This is a much later date than recommended by most authorities (most successful beekeepers strive to treat by mid-August), as viruses can go epidemic in colonies with high mite levels in late summer, leading to midwinter collapse, as occurred in your colonies.
Q: Could you please explain why you waited so late to treat for varroa?
Your choice of Apistan strips as a mite treatment is of interest, since the mites in your colonies would be expected to be descended from those present in the original package bees. Mites in most commercial operations exhibit high resistance to the active ingredient of Apistan.
Q: Do you have any data on what the actual mite levels were in the colonies in October, and whether the strips were actually effective at reducing the mite infestations to below economic thresholds?
Questions on unpublished data on colony strength
You mention that “notes were also made of the number of frames of adult bees observed.”
Those data would be of great interest, and allow the reader to track any treatment effects upon the colony size over time. Unfortunately, the results are not included in the paper. All the treated colonies survived for at least three months after treatments were completed. I’m curious as to when adverse effects due to treatment became apparent.
[In the study, poisoning the colonies all through late summer and early fall likely hampered the ability of the colonies to prepare a healthy population for winter.]
Q: Could you share your data on cluster size? I’m especially interested in how colony cluster size was affected during the initial four weeks of treatment at true “field relevant” dosages of imidacloprid. Of note is that the initial field-relevant doses of imidacloprid appeared to stimulate broodrearing in proportion to the dose!
Q: Do you have any comments about this surprising finding?
Questions on stored honey
In the trial, you fed a large amount of HFCS to the colonies (approximately 71 lbs). I’m very curious about the apparent delayed effect due to the feeding of treated syrup.
Q: Did you test any of the stored honey in the dead colonies for the presence of imidacloprid?
In late December, you began feeding supplemental sugar in patty form.
Q: If the colonies contained adequate stores, why was this necessary?
Q: Do you have data on how much supplemental sugar was consumed by the various colonies during winter, and did this correlate with either treatment or mortality?
Could the HFCS that you used have been the cause of mortality?
You state: “the systematic loss of sealed brood in the imidacloprid-treated and control hives may indicate a common stress factor that was present across all 4 apiaries.”
I heartily agree, especially since one would expect nutritional and pathogen factors to vary from apiary to apiary!
I feel that it may be premature to reach the conclusion that imidacloprid-induced CCD occurred until you determine the cause of the reduced brood rearing, which you observed was “vastly different from that normally seen in honey bee hives” in your area. Perhaps the reason was that the HFCS that you fed in the trial was a poor bee food, independent of any pesticide residue.
In your trial, you fed an extraordinary amount of HFCS to the colonies (13 feedings of ½ gal at 11 lbs per gallon = 71.5 lbs of HFCS). Few beekeepers that I know of have ever fed this amount of HFCS to colonies.
You cite a study by Dr. LeBlanc from the Tucson ARS lab, who found that storage of HFCS in warm conditions, especially in metal containers, could result in toxic levels of HMF formation.
Q Could you please tell us how you stored your HFCS and whether you tested to confirm that HMF was not present in toxic levels in your syrup toward the end of the trial?
LeBlanc and his coworkers also determined that there were no imidacloprid residues in any of the several brands of HFCS that they tested! Of note though is that they found that some brands of HFCS caused increased mortality in caged bees. You state that you used “food-grade HFCS.”
Q: Was it a brand that is normally fed to colonies by beekeepers in your area as winter feed, and do you have previous experience with feeding this brand to your colonies? Could you please tell us which brand you used, as this is of great interest to beekeepers?
Q: Did you perform any cage trials to see whether that brand of HFCS exhibited toxicity to bees?
Q: I’m curious as to why you did not feed sucrose syrup as a control group, to see whether the HFCS that you used caused colony morbidity for reasons other than your hypothesized insecticide contamination. Comments?
You state: “the delayed mortality in honey bees observed in late winter months remains puzzling.” I agree that this is the key issue in your study. The question is, was it due to the dosing with extremely high levels of the insecticide, the prolonged feeding of HFCS, or to nosema or varroa buildup in the colonies. Without eliminating the other plausible causes, I feel that it is premature to place the blame for the observed colony mortality solely upon the insecticide.
Questions on dwindling of both test and control colonies
Regarding Figure 1 (brood area tracking), you mention that there were no significant differences in broodrearing due to treatment. I find this point noteworthy, as well as surprising, given the high dosages of imidacloprid given!
Q: Any comments?
You state: “It should be noted that the steady decreasing trend of sealed brood during the summer months as observed in this study is vastly different from that normally seen in honey bee hives residing in the central Massachusetts area.”
It appears that all the colonies, including the controls, were suffering from some sort of morbidity. The most likely suspects would be the poor nutrition of the HFCS (independent of the added insecticide), nosema, or the varroa/virus complex.
Although you were monitoring brood areas weekly, and clearly noted that something was apparently wrong in all colonies, you waited until October 5 to begin any standard parasite treatments.
Q: Could you please explain why?
Figure 2 (the chart of colony survival) is striking, and clearly shows that colonies fed very high dosages a pesticide died sooner than those not fed pesticide. I do not find the results surprising. What would be of interest is the starting cluster sizes of the colonies going into winter cluster. Smaller colonies are well known to exhibit poorer winter survival than strong colonies.
Q: Did the treated colonies enter the winter with smaller cluster sizes, and could this be the reason for their early mortality?
Did you actually observe CCD, or mere dwindling
You state: “The magnitude and the pattern of honey bee hive loss during the winter months in this study resemble the reported symptoms of CCD.”
Frankly, this is where the CCD researchers that I’ve spoken with have questions. They do not find the “symptoms” that you reported to be consistent with the markers for CCD!
Q: Did any of the members of your team have any actual previous experience with observing CCD in the field?
The CCD Working Group deliberately named CCD colony collapse to distinguish it from colony dwindle. vanEngelsdorp (2009) suggests an operational case definition of CCD “characterized post hoc by a common set of specific symptoms: (1) the rapid loss of adult worker bees from affected colonies as evidenced by weak or dead colonies with excess brood populations relative to adult bee populations; (2) a noticeable lack of dead worker bees both within and surrounding the affected hives…”
To the contrary, you describe the dwindling of the treated colonies in your study as: “the strength of hives treated with the highest imidacloprid dose appeared to be weakening as observed by smaller clusters and frozen dead honey bees scattering (on snow) in front of the hives.” You also show in Figure 3 a lack of sealed brood in a dead treated hive.
Since the “symptoms” that you report do not appear to match those that distinguish CCD, I cannot fathom how you can conclude: “Data from this in situ study provide convincing evidence that exposure to sub-lethal levels of imidacloprid causes honey bees to exhibit symptoms consistent to CCD months after imidacloprid exposure.”
Q: Could you please explain how you can state that the signs that you observed were “consistent” with those of CCD, rather than being typical signs of dwindling due to parasites or poor quality feed?
You state: “Snow usually fell between weekly hive examinations making the observation of scattered dead honey bees in front of individual hives noticeable. Although this observation is not quite reminiscent of the reported CCD symptoms…”
“Not quite reminiscent” is certainly an understatement—either you observed the signs of CCD or you didn’t! In my personal beekeeping experience in a cold winter area, scattered dead bees on snow in front of hives during winter are normal, due to aging bees flying out to die, and is indeed not at all “reminiscent” of CCD symptoms.
Q: Why do you bring up this observation—is it not normal in your area to see dead bees in the snow following flight days during winter?
It appears that you consider the lack of dead bees in the hive to be unusual. When I check the weather history for Worcester for the winter of 2010, it appears that there were an adequate number of days warm enough for bee flight through early December to allow virus- or nosema-infected bees to fly off to die.
So I’m not clear as to whether the dwindling of clusters reflected the normal self removal of sick, aged, or infected bees, or was due to unusual flight behavior in cold weather due to imidacloprid exposure (which your discussion hints at).
Q: Do you have any observations that could help clarify when the bees flew off?
Your definition of “sub-lethal”
You state: “Data from this in situ study provide convincing evidence that exposure to sub-lethal levels of imidacloprid in HFCS causes honey bees to exhibit symptoms consistent to CCD”
I think that everyone would be in agreement that the doses used during the first 4 weeks of feeding would be considered to be “sub-lethal.” You did not report any adverse effects from those dosages, as expected.
But then, without explanation, your team ramped up the doses considerably. Yet you still claimed that they were “sub-lethal.” I must question whether the dosages that you used in 9 weeks of late-summer feeding would be considered to be “sub-lethal.”
Your team added to the syrup for each weekly feeding doses of imidacloprid ranging from 51.9 μg to1038 μg.
You report that each colony covered about 20 frames. There are typically about 1750 bees per covered frame, so that would suggest colony populations in the range of 35,000 bees.
You do not report how quickly the colonies emptied their feeders, but in my practical beekeeping experience, a half gallon of syrup is typically consumed in less than 24 hours, so unless you tell us otherwise, we can assume that the administration can be treated as 24-hr dosings.
Cresswell (2011) in his meta analysis of imidacloprid toxicity trials, found that observable toxic effects began to occur at doses exceeding about 2 ng per bee. Bayer scientist Maus (2003) states that acute oral LD50 of imidacloprid to honey bees is as low as 40 ng/bee.
Let’s convert your four dosing regimines to ng/bee:
51.9 μg/colony = 51,900 ng/colony = 1.5 ng/bee
103.8 μg/colony = 103,800 ng/colony = 3 ng/bee
519 μg/colony = 519,000 ng/colony = 15 ng/bee
1038 μg/colony = 1,038,000 ng/colony = 30 ng/bee
So by my arithmetic (based upon previously published research), even your lowest rate of dosage gave a marginally toxic dose of imidacloprid to each and every bee in the hive, and your highest dose approached the LD50 for all the bees in the hive!
This is a key question. It appears to me that the high doses of imidacloprid that you used hardly be considered to be “sub-lethal.”
Could you please explain how your team can consider such concentrations to be “sub-lethal”?
Your hypothesis and conclusions
Quite a number of trials worldwide have been performed to apply Koch’s third postulate in an attempt to create disease in healthy bee colonies by the feeding of field-relevant doses of neonicotinoid insecticides. To date, that goal has eluded all other research teams other than yours!
For example, in a similar but more thorough study (Faucon 2005) the conclusion was that “In any case, during the whole study, mortality was very low in all groups, with no difference between imidacloprid-fed and control colonies.”
Q: Could you please elaborate as to why you feel that your results were different than all other trials to date? [this is normally done in the Discussion section of a scientific paper].
You suggest that: “The survival of the control hives managed alongside with the pesticide-treated hives unequivocally augments this conclusion.”
“Unequivocally” is a pretty strong statement! In actuality, your Figures 1, 2, and 4 suggest that the control hives were suffering from serious morbidity, and on the same path to mortality as the treated hives, only to be rescued by the infusion of pollen in spring! Note that the control group suffered 25% mortality (which hardly constitutes “survival”), which raises serious questions about any conclusions to be drawn.
Q: Could you please provide your cluster size observations to help the reader to determine the degree of morbidity in the control colonies relative to that of the treated colonies?
Q: Did you inspect the brood combs of the deadouts for guanine deposits, which would indicate that varroa was present at high levels as the colonies dwindled?
Q: Did you sample any of the dead bees in the snow for nosema?
Since all colonies in your trial suffered from unusual morbidity, the question is raised whether such morbidity was due to the unnatural feeding of the particular brand of HFCS that you fed to the colonies.
You state: “It is likely that CCD was caused by feeding honey bees with low levels of imidacloprid in HFCS throughout their lifecycle in which toxicity occurred during the larval/pupal stages and was later manifested in the adult honey bees.”
I find a paucity of published data on the toxicity of imidacloprid to bee larvae, or whether residues in syrup even make it into the larval food. [The neonicotinoids are apparently virtually nontoxic to larvae (Lodesani 2009); Piotr Medrzycki, pers comm]
Q: Could you please cite research to support your claim that “it is likely” that “toxicity occurred during the larval/pupal stages”?
Q: Similarly, could you please cite research to support your claim that “it is likely” that any such toxicity would be “later manifested in adult honey bees”?
SciTech Daily’s article  on the paper says, “Strikingly, said Lu, it took only low levels of imidacloprid to cause hive collapse — less than what is typically used in crops or in areas where bees forage.”
In actuality, it appears to me that the initial, field-realistic, levels of imidacloprid that you feed the first four weeks did not cause observable adverse effects.
Q: How can you state that “it took only low levels of imidacloprid to cause hive collapse” when in your own paper you refer to it as “high imidacloprid dosing”?
Then even after feeding clearly lethal levels of the insecticide for an additional nine consecutive weeks, you still did not observe colony mortality!
It was only three full months after you ceased feeding the insecticide that you observed the first mortality, following a period in which the “systematic loss of sealed brood [in all] hives may indicate a common stress factor that was present across all 4 apiaries.”
[The authors state: “Considering the sensitivity of honey bees to imidacloprid as demonstrated in this study.” Actually, no such “sensitivity” was demonstrated at all! Even the lowest fed dosage (20 ppb) is about 5-20 times higher than that commonly found in nectar, and the other three doses were far higher--it is amazing to me that the colonies were not killed outright! Yet no treated colony apparently showed any ill effects even after 13 weeks of continuous feeding with insecticide-spiked syrup!]
An alternative explanation for the results
Your proffered hypothesis is that: “Data from this in situ study provide convincing evidence that exposure to sub-lethal levels of imidacloprid in HFCS causes honey bees to exhibit symptoms consistent to CCD 23 weeks post imidacloprid dosing.”
To many, your evidence is actually less than convincing.
I suggest an alternate hypothesis that all the colonies were on a downhill track by late summer, and dwindled due to either HFCS toxicity or parasite loads, and that the feeding of unrealistically high doses of an insecticide merely accelerated the decline of the treated colonies.
Q: Do you have any evidence that would help to falsify this alternative hypothesis?
Feel free to make any additional comments at this point. Thank you in advance for taking the time to answer these questions for the benefit of the beekeeping community!