After hearing the horrible news that Laura Hymas had died on the same day that I found out that the pro-quackery “health freedom” Alliance for Natural Health (ANH) was supporting a federal “right to try” bill, I thought it would just be a one-off post about Burzynski, his allies, and the human toll exacted by his cancer quackery. No such luck. The reason is that yesterday morning I awoke to e-mails and Tweets from multiple colleagues and bloggers making me aware of an article published in a journal that (once again) I had never heard of, Child’s Nervous System. The article is by—surprise! surprise!—Stanislaw Burzynski and the usual suspects at the Burzynski Clinic and Burzynski Research Institute and entitled The response and survival of children with recurrent diffuse intrinsic pontine glioma based on phase II study of antineoplastons A10 and AS2-1 in patients with brainstem glioma.
My first reaction was: Hmmmph. It looks as though Burzynski finally found a journal editor naive or ignorant enough to publish one of his clinical trials. Then I looked at the abstract and realized that I had jumped to a conclusion. Burzynski hasn’t published one of his phase II trials at all. He’s published only less than half of a phase II trial, as you will soon see. In fact, he’s published exactly 42.5% of one of his phase II clinical trials.
Looking over the methods, I noted that this is trial BT-11. That means that it’s one of the 72 clinical trials submitted by Burzynski in the mid-1990s in order to take advantage of FDA willingness to consider approving his clinical trials. This was a willingness forged in the furnace of Rep. Joe Barton’s constant flogging and investigating of the FDA and his frequent dragging of then FDA director David Kessler in front of his committee for some tender loving rhetoric about his “persecution” of Burzynski, interspersed with crying families of cancer patients who were afraid that the FDA might actually manage to convict Burzynski. Again, remember, these families honestly believed that Burzynski was responsible for their loved ones still being alive and that Burzynski was the only doctor who could save them from death due to their various advanced tumors of the brain and other organs. It’s not the patients that I castigate, rather, it’s Burzynski’s cynical use of these patients as “human shields” against the FDA. In any case, let me just refresh your memory about these 72 clinical trials, quoting the immortal words of Burzynski’s lawyer, Richard Jaffe:
CAN-1 [a “wastebasket” clinical trial by Burzynski approved by the FDA and earlier described by Jaffe as an “artifice, a vehicle we and the FDA created to legally give the patients Burzynski’s treatment”] allowed Burzynski to treat all his existing patients. That solved the patients’ problems, but not the clinic’s. A cancer clinic cannot survive on existing patients. It needs a constant flow of new patients. So in addition to getting the CAN-1 trial approved, we had to make sure Burzynski could treat new patients. Mindful that he would likely only get one chance to get them approved, Burzynski personally put together seventy-two protocols to treat every type of cancer the clinic had treated and everything Burzynski wanted to treat in the future…Miracle of miracles, all of Burzynski’s patients were now on FDA-approved clinical trials, and he would be able to treat almost any patient he would want to treat!
Now, more than 15 years later, we finally see one of these 72 trials published—sort of. There is far less to Burzynski’s clinical trial than meets the eye. After reading the study, my reaction to it was: Huh? That’s all you could come up with in over 15 years? Really?
I’ll take care of the formalities first. From the methods:
The study was designed as a single-arm, two-stage, phase II trial of ANP as monotherapy. The study was listed by the National Cancer Institute (NCT00003459). It was supervised by an independent Institutional Review Board (BRI-IRB, BCBT- 11). The study was performed
This “independent” IRB is, of course, the same IRB that is chaired by an old crony of Burzynski’s from Baylor who also happens to be the chair of the board of the Burzynski Research Institute. It’s also the same IRB that was recently roundly condemned in an FDA warning letter for abusing the single patient IND process, failing to provide adequate informed consent, and failing to protect patients interests and make sure that the risks of BRI clinical trials are minimized.
Of course, the line in the paper that leapt off the page at me was this one:
The protocol permitted admission of patients with brainstem glioma for whom standard curative treatments are not available. A total of 40 patients were enrolled, but the scope of this paper has been limited to the 17 RPDIPG patients.
So why isn’t Burzynski reporting on the other 23 patients? This is what I mean when I say that Burzynski is reporting less than half of a phase II trial: 17 patients out of 40, which equals 42.5% of the patients on that trial. RDIPG, by the way, stands for “recurrent pediatric diffuse intrinsic pontine glioma.” I also note that the inclusion criteria for the original BT-11 trial include “histologically confirmed (except if medically contraindicated) brain stem glioma that is unlikely to respond to existing therapy and for which no curative therapy exists.” So why limit it to just 17 patients? It’s not explained in the manuscript other than the sentence above. I’m also puzzled by the choice of dosage, in which the infusion rates of antineoplaston therapy were scaled according to the patient’s age, rather than the more standard method of calculating overall daily dose based on either body weight or body surface area and then simply administering that dose. It’s not necessarily wrong, but it’s nonstandard.
It’s also important to note that this is not a randomized trial. There is no control group. It’s more like a combined phase I/II trial than a strictly phase II trial given its lack of randomization and control group plus its dose escalation design. Again, this is not wrong; it’s how many early phase II trials are done. It’s just that, even if the trial were promising, it would not in any way constitute definitive evidence that antineoplastons are efficacious against brain tumors. In any case, I think I’ll just cut to the chase here and show you the results. Here’s Figure 4, a Kaplan-Meier survival curve showing overall survival (OS) and progression-free survival (PFS).
Not particularly impressive, is it? It sure doesn’t look like any sort of miracle cure. However, it should be noted that DIPG is a horrible tumor, and the median survival tends to be on the order of several months, with survival beyond two years rare—rare, but, as I note, not “never,” as Burzynski claims. Moreover, as dismal as this survival curve is, in fairness, one has to note that it’s better than typically reported for DIPG. (Yes, DIPG is just that bad.)
Still, there’s some rather deceptive reporting going on there. No, it’s not outright lies. However, it’s reporting that fails to put results in context. For example, Burzynski reports a complete response in 6% of patients. That would be one patient out of seventeen. That one patient, it would appear, is a patient with a grade I pilocytic astrocytoma. This is a tumor that is not considered to be malignant. No, seriously. It’s generally not considered a malignant tumor:
Juvenile pilocytic astrocytoma (JPA) is a rare childhood brain tumor. In most cases, the tumor is a benign, slow growing tumor that usually does not spread to surrounding brain tissue. Symptoms of a JPA will vary depending upon the size and location of the tumor. Most symptoms result from increased pressure on the brain and include headaches, nausea, vomiting, balance problems and vision abnormalities.
So, in reality, excluding this one patient Burzynski’s long term survival result, even among these seventeen patients, is, as one would expect for DIPG, zero. Not surprisingly, that same patient is the one who had what was described as a “complete response” (CR). Excluding that patient, as would be appropriate, makes Burzynski’s CR rate zero as well. In fact, there were two cases of pilocytic astrocytoma included with this group, and the other patient with this tumor type was reported as a partial response (more the 50% tumor shrinkage). So, even in this apparently cherry-picked group of patients, Burzynski’s results are not what they seem and not as impressive as he presents them. That’s leaving out the toxicity:
Safety assessments were analyzed based upon the total number of enrolled patients (n=17). Grade 4 toxicities including hypokalemia and fatigue occurred in 6 % and hypernatremia in 18% of the group. Grade 3 fatigue and urinary incontinence occurred in 6 % and somnolence in 12 %. In patient 2 (Table 2), grade 4 hypernatremia was detected when he was on mechanical ventilation in the intensive care unit. This patient received terminal care and was disconnected from the ventilator upon request of the members of his family. His attending physician determined brain tumor as the cause of death.
Remember the definition of grade 4 toxicity. According to the Common Terminology Criteria for Adverse Events (CTCAE), it’s toxicity that is potentially life-threatening, and grade 3 is severe, as in requiring treatment or even hospitalization. I’m also not convinced about this hypernatremia in that it’s listed as grade 4, but then Burzynski dismisses the patient’s death as being due to the brain tumor. Yet, clearly even from this description it seems as though the development of grade 4 hypernatremia is what prompted the family to decide to stop treating him and switch into the palliative care mode, disconnecting him from the ventilator. In any case, if you add up the toxicities, grade 3 or 4 toxicities occurred in 42% of patients. Contrary to how Burzynski’s treatment is represented, both by him and his supporters, this is hardly “nontoxic” therapy.
Finally, leave it to Burzynski’s supporters to sabotage him in their enthusiasm to “prove” what a genius he is. The ANP Coalition—remember these guys?—published a blog post the other day announcing with pride the publication of 17/40 (or 42.5%) of Burzynski’s clinical trial. In it, they exulted:
The results of this study depict a high level of efficacy along with a more than acceptable tolerance of ANP.
One of the article’s sterling successes is Jessica Ressel. You can meet Jessica under our website’s “Meet the Miracles” button.
Who remembers Jessica Ressel? I do. In fact, she played a prominent role in the very first movie made by everyone’s favorite Leni Riefenstahl to Dr. Burzynski’s—oh, never mind. I’m referring, of course, to Eric Merola’s first Burzynski “epic” that portrayed Burzynski as a misunderstood genius and “brave maverick doctor.” In fact, her diagnosis of pilocytic astrocytoma is very consistent with what her tumor looked like on imaging. Indeed, even two and a half years ago I thought that it looked like a small, odd tumor. Indeed, Burzynski’s description of the tumor in his paper does not jibe with what I saw when I watched Merola’s first movie about him. There, the tumor was small. In the paper, the the tumor was described as “tumor involving 72 % of pons at the baseline.” Go back and look at the images I took from the film and showed in my original post on Merola’s first movie. Does the lesion look as though it takes up 72% of any structure? Not to me, it doesn’t. It’s easily covered by a yellow “radiologist’s mark.” I will admit that I’m not a radiologist, in particular a neuroradiologist. Even so, the lesion shown on the scan that Eric Merola included in his medical records for his movie is small. Even a “dumb surgeon” such as myself can recognize that, and the largest measurement ever recorded for the tumor was 1.7 cm, with many times the measurement being recorded as well under 1 cm. This same “dumb surgeon” also recognized that there was something very strange about the tumor size measurements recorded during Ressel’s treatment. Again, go back and read my review if you want the details. (I love being able to say that, given that I wrote it two and a half years ago.) Suffice to say, Ressel’s case is not convincing evidence that antineoplastons are effective against DIPG.
The bottom line is that this “study” is nothing more than a typical ploy by Burzynski and his allies to convince the rubes that, alone of all the scientists studying such seemingly untreatable tumors, Burzynski can offer a chance of curing them. The problem, of course, is that there’s no evidence that he can. He’s only presenting 43% of his patients in this study. My guess is that the rest of the patients did poorly, and if that’s the case, then his real survival rates are probably less than 50% of what he is reporting because he’s excluded them from the denominator. That would bring his results right into line with everyone else’s—or even make them worse than average.
Then there are the scans shown in Figures 2 and 3. Look at them. They show different sections of the brain. (Use the eyes to compare.) Given that, they don’t actually demonstrate whether or not there is a response. There are a number of other oddities, too, such as how long it took to accrue so few patients, why the study is only now being published seven or eight years after the most recent data reported, and the like. Come to think of it, this isn’t even really 42.5% of a clinical trial, and even this undoubtedly carefully cherry picked segment of one of Burzynski’s 72 phase II trials is completely underwhelming.
I’ll conclude by pointing out that, upon seeing this study, I wrote an e-mail to Concezio Di Rocco, the editor of Child’s Nervous System, expressing many of these concerns in a less “insolent” fashion. Here was his response:
Thank you for your letter. I have already asked some eminent neuroncologists to write a comment in the direction you suggest.
Bob Blaskiewicz also wrote an e-mail to the editor, and this was the response he got:
I have invited eminent neurooncologists to write a comment to be added to the articles. Unfortunately the reviewers of the journal failed to provide their promised evaluation so that after several months there were “no negative comments” to justify rejection. Now I look for receiving comments from Canada and UK to be published in the journal. Should you be willing to contribute you are welcome.
I’m not entirely sure how to interpret this, but this seems to be saying that Burzynski’s article was not peer-reviewed. Basically, it appears that Burzynski submitted his article, and the editor, not getting any comments back from his peer reviewers, just decided to publish it. This suggests that the policy of his journal is that the default action for a manuscript is to publish unless there are negative comments. I’ve never heard of a journal with such a policy before, which makes me wonder if I’m missing or misinterpreting something here. Either way, I’m not surprised. The only way Burzynski can publish his tripe is if he slips his study into a journal with—shall we say?—less than rigorous editorial standards.
Same as it ever was, which is why my final reaction remains: Hmmmph. It looks as though Burzynski finally found a journal editor naive or ignorant enough to publish one of his crappy clinical trials.
47 replies on “Stanislaw Burzynski publishes 42.5% of one clinical trial”
How can this be a real medical journal? The reviewers did not submit any comments? Really? How does anything get reviewed at that journal? Then they publish the paper because of a lack of criticism? Well, I’ve got a bridge in Brooklyn that I’d like to sell them.
How can this be a real medical journal? The reviewers did not submit any comments? Really? How does anything get reviewed at that journal? Then they publish the paper because of a lack of criticism? Well, I’ve got a bridge in Brooklyn that I’d like to sell them.
Unfortunately the reviewers of the journal failed to provide their promised evaluation
I can testify from my own experience that there is far too much of this going on. But the correct way to handle this scenario is to send the paper out to another reviewer, or failing that for the editor to review the paper himself if he feels qualified. Yes, the editor does have discretion to accept the paper even if the reviewers recommend otherwise, or do not provide a recommendation. However, it should have been reviewed one way or another.
Although the editor is the one primarily responsible for publishing this paper, I will apportion a share of the blame to the people who agreed to review this paper and then failed to do so. Hey, I understand you’re busy. But if you can’t review the paper promptly, the correct thing to do is to inform the editor that you will be unable to review the paper in a timely fashion.
why the study is only now being published seven or eight years after the most recent data reported
It would be interesting to know if the paper had been submitted to any other journals before it was finally printed, and if so, how many.
So even with Burzynski carefully selecting a minority of patients studied (by what criteria?), the outcome is no better than and quite possibly worse than with standard care (discarding that “ringer” case), and with marked toxicity to boot.
If this is the best “success story” he can come up with, no wonder his phase II trials go unpublished.
I am not a scientist, so this may be an ignorant question. However — my understanding was that percentages are used for clarity, e.g., “31% responded” is clearer than “114 out of 372 responded”. In this case, though, there were only 17 cases, so each 6% (approximately) was one case and I was mentally converting each percentage to cases.
The law of large numbers doesn’t apply here; putting everything else aside, if you applied the treatment to 1700 patients, you would not expect to see the same percentages.
So, my ignorant question: is it normal to use percentages in such a small group and, if so, would you expect the number of cases to be given also, as “6% (1 patient) experienced Grade 4 hypernatremia”?
Since the FDA documented that Burzynski has failed to report adverse events, it’s likely that the toxicities discussed in this paper are understated.
Furthermore, the interpretations of the readings (especially the baseline ones) may be confounded by the conventional therapies administered to the patients,
@ Michael Finfer
Sounds like it.
Maybe one of the editors got recently married and liked so much the ceremony he decided to adopt it as a review process.
“Whose who oppose this article, speak now or stay forever silent!”
I suspect that Ivan Oransky and Adam Marcus at Retraction Watch would be interested in an EIC bluntly admitting that a paper was published because the reviewers failed to timely get their work done.
is it normal to use percentages in such a small group and, if so, would you expect the number of cases to be given also, as “6% (1 patient) experienced Grade 4 hypernatremia”?
I think standard practice is to make clear how large the sample size is, and then quote percentages thereafter, knowing that anybody who really wanted to convert it to a raw number of cases could do the necessary multiplication. What Burzynski was hoping (and was successful at the editorial review stage) was that nobody would notice how small his sample size was, or that more than half of his potential sample size was discarded for dubious reasons. Possibly for similar reasons, several of the percentages were quoted to the nearest 0.1%–that’s a sensible thing to do with a sample size of a couple hundred or larger, but not for N = 17.
Was Joe Barton the boot licking congress critter that apologized to BP after Obama strong armed them into paying more than the least they could get away with for the Macondo blowout?
It looks like it:
What a reprehensible waste of air. No wonder he shills for Burzinsky.
How can he not report the outcomes for all the patients that enrolled in his trial and then not even explain it? This is horrible journalistic integrity and peer review to allow such a “paper” the light of day.
The man obviously has no shame. Any paper where they throw out over half the data should automatically be rejected with the question ‘where’s the rest of your data’? This should never have been published and is deeply misleading to people who don’t understand scientific publications or statistics very well. Saying 6% of patients had severe adverse events seems really reassuring when you are thinking they studied a large number, in a trial this small not so much. I really wish FDA had just shut him down. All of this false hope and shrill cries for ‘freedom’ on the internet made me really upset. The fact that my home state of TX appears to be Mecca for woo-meisters makes me hopping mad.
“Saying 6% of patients had severe adverse events seems really reassuring when you are thinking they studied a large number, in a trial this small not so much.”
Especially when you wonder how many adverse events were suffered by the excluded 23 patients and if, perhaps, they were excluded to lower the rate of adverse events.
I have to wonder if a lot of reviewers are nervous about rejecting papers, or are unlikely to read ones that appear “poor” right from the start and push the responsibility to other reviewers?
This should never have been published and is deeply misleading to people who don’t understand scientific publications or statistics very well.
I suspect that the average reviewer doesn’t realize that papers like this are really propaganda targeted at non-scientists. Not that that’s any excuse, mind you.
From a nobody like Burzynski? I doubt it.
In that case, they shouldn’t have agreed to review the paper in the first place.
Papers submitted for review are anonymous, stripped of any identifying information, or at least as much as possible. While it is pretty clear who runs antineoplaston town, it doesn’t become absolutely obvious until late in the paper.
If I remember correctly, most journals submit the articles to at least twice as many reviewers as it needs to pass review, because sometimes the reviewers just don’t have time, expertise or some other reason.
Are you sure? (PDF)
Papers submitted for review are anonymous, stripped of any identifying information, or at least as much as possible.
Some journals do that but not all, and in particular, the journals I am most familiar with do not.
I have to wonder if a lot of reviewers are nervous about rejecting papers
This is one reason why reviewers are anonymous, at least during the refereeing stage (some journals allow reviewers to self-identify after the fact). Otherwise junior scientists would be justifiably afraid to even suggest significant (even if feasible) revisions to a paper by a prominent senior scientist. It’s sometimes possible to guess the identity of the anonymous reviewer (e.g., if the reviewer tells me I should cite some ANP studies that would lead me to think Dr. B is the reviewer), but the guesses are not always 100% accurate. I’m sure some reviewers would prefer not to recommend rejection (after all, some trash does slip past peer review), but many are not–I for one am not afraid to reject papers that I think are too seriously flawed to merit publication. And Burzynski is not so prominent that anybody who doesn’t already work for him would have any reason to fear his wrath. (Those who are affiliated with the same institutes as the paper’s authors are not supposed to serve as reviewers, for obvious reasons.)
Just did a Google search. This is the official journal of the “International Society for Pediatric Neurosurgery”. According to the society’s website, they have 350 members from 40 countries- an average of less than nine members per country, and the journal is published annually. Maybe they don’t have many referees to ask? Or get many papers sent to them?
It’s hard to get the lay of the land quickly, but I’d guess that single-blind reviewing is the norm.
OT: Does anybody know what ever happened to Virginia Trimble’s ApXX reviews?
I bet there’s a simple reason that there are so few members, and that’s because there just aren’t that many pediatric neurosurgeons out there.
Re: Reviewing medical manuscripts
I’ve reviewed for many journals over the years, and I’ve never seen a manuscript blinded to me. I always know who the authors are. The vast majority of reviewing in the biomedical literature is single blind.
I’m sorry if this is a stupid question but how could they even include a grade I pilocytic astrocytoma as DIPG?
This is one reason why reviewers are anonymous, at least during the refereeing stage (some journals allow reviewers to self-identify after the fact).
The Frontiers journals follow the named-reviewers policy, so if you recommend a paper for publication, you own the embarrassment if it later turns out to be total hooey.
There used to be one argument for anonymous review, that it would reduce the incentive for log-rolling… but with everything searchable on-line, any egregious mutual backscratching among named reviewers would be easily spotted, so the argument is noncupatory.
DIPGs (when biopsied) occur most commonly as grade III or IV, on occasion as grade II. It seems to be quite rare for such a tumor to manifest as a DIPG but on biopsy show features of a pilocytic astrocytoma.
Regardless, it comes across as misleading (to be kind) for Burzynski to include such a tumor in his series of DIPG cases.
How could a review be double-blind? Sure, they could take the author'(s)’ name off—but in a lot of cases they’re going to be citing their own work. The editor could cover those up, I suppose, but when you go online to see the paper in question, you’ll see the author'(s)’ name(s).
By hoping for the best.
With this one stroke, Stan Burzynski has attained .0425% of the credibility of the average cancer researcher.
@John McC: The universe of potential reviewers for this journal may well be small, and that would be all the more reason to fear that the authors could successfully guess the reviewer’s identity (I’ve done it myself, and the number of potential reviewers of my papers is an order of magnitude larger than in this case). But I’m not aware of any journals that actually prohibit an editor from appointing himself to review a paper–the reason the editor isn’t usually a reviewer is to prevent his (often uncompensated) workload from getting too high. In cases like this, however, there may have been no other alternative to publishing the paper without its being reviewed (which should never happen, but apparently did in this case).
@HDB: There are still issues of power asymmetry. Early-career scientists are usually not in secure positions, so their fears of senior scientists retaliating against them for unfavorable paper reviews have a rational basis. That’s particularly true in a funding environment where one unfavorable comment can sink your proposal (as is true in the US, even more so than when I was a grad student). But you don’t want to exclude those junior scientists from serving as reviewers. Anonymity may not be the best solution to this problem. OTOH, it may be the worst possible solution apart from anything else that has been tried.
“I’ve reviewed for many journals over the years, and I’ve never seen a manuscript blinded to me.”
That’s odd, I’ve always been presented with blinded ones, devoid of author’s name, at the very least. Wouldn’t you think that would lead towards author bias?
Wouldn’t you think that would lead towards author bias?
As others have pointed out, you can usually figure out who the authors are from the topic and citation patterns. It’s like the “guess the referee” game, but easier because you generally have a great deal more material to go on. So many journals simply don’t bother with the charade.
1. On double blinding: someone looked at this & found that when a paper was double-blinded, the reviewers correctly identified the authors about 40% of the time (I’m tempted to suggest 42.5%, but IIRC it was higher. And I’m not going to check for the reference – having wine & pizza with my wife).
2. It’s the editor who decides on the fate of a paper, so if they get no reviews, they should FUCKING READ IT THEMSELVES.
I know the problems with getting reviews far too well, but still. If you don’t get reviews, review it yourself. At the very least you buy yourself time to find reviewers
I am curious of what you might have to report on the DCA trials at MD Anderson in the usa and medicor cancer treatment center in Toronto, about Dr. Akbar Kahn, Dr. Michelakis, about dichloroacetate? I’m still alive, had a six month prognosis in 2006 but hey, I took DCA and it’s 8 years later! Thanks to DCA, I am alive and well! I was stage 4e mantle cell lymphoma, not something easily treated! I love the way the American Cancer society blog has stated that dichloroacetic acid (C12CHOOH) is the same as dichloroacetate (C12CHOONa). It’s not! The acid is poisonous, the sodium is harmless to healthy human cells but works on the mitochondria of cancer cells so they can die a natural cell death. You need to read up on the RECENT reports. It isn’t snake oil or I wouldn’t be here today!
Ms. Dowell, there is a search box on top of this page. You might try reading what pops up with DCA:
judy dowell @37
It’s not C12CHOOH/Na – it’s CHCl2COOH/Na, or if you must Cl2CHCOOH/Na (I’m not going to attempt to use subscripts here). The “C12” you put in there is actually the “dichloro-” part of DCA.
Here is a link to an Orac’s in depth analysis from 2010:
(The search box yields as the most recent post one in May 2011, but this one is more comprehensive)
If you want anyone to check out “the RECENT reports,” why don’t you post links?
I wouldn’t read too much into that. Biochemists tend to use the words for acids and their salts interchangeably, so serum urate and serum uric acid levels, for example, are the same thing.
Sodium dichloroacetate is not harmless to healthy human cells. At high enough doses it is neurotoxic and can cause neuropathy. It does this by inhibiting pyruvate dehydrogenase kinase, thus blocking anerobic repiration. This means that any cells with a limited oxygen supply, however healthy, will be unable to metabolize glucose, essentially starving them. This isn’t an entirely harmless drug as you suggest.
The thing is, of course, that DCA is definitely bad for cancer cells. But like most chemotherapeutic agents, it is also bad for normal cells. Cancer cells and normal cells are very, very similar in their inner workings, so it’s tough to come up with a drug therapy that will harm the one while sparing the other.
Wouldn’t it be fun for someone with the proper medical qualifications, such as Dr. Gorski, to be given the opportunity to cross-examine Burzynski and the editor of this rag, of course, recording the whole thing for posting on You Tube? .
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