Two things have reminded me that it’s been a while since I’ve written about Stanislaw Burzynski, nearly five months, to be precise. First, on Wednesday evening I’ll be heading to the city where Burzynski preys on unsuspecting cancer patients, Houston, TX, to attend this year’s Society of Surgical Oncology meeting to imbibe the latest research on—of course!—surgical oncology. (If you’ll be attending the meeting, look me up. If you’re in Houston and want to have a meetup, I might be able to pull it off.) Second, you, my readers, have been telling me there’s something I need to blog about. This time around, my usual petulance at being told I must blog about something notwithstanding, I’m inclined to agree (more later). It is, after all, Stanislaw Burzynski.
The last time I wrote about Burzynski was when McKenzie Lowe, an unfortunate child with a particularly deadly form of brain cancer known as diffuse intrinsic pontine glioma (DIPG) whose parents lobbied to allow her to be treated with his antineoplastons when his clinical trials were still on clinical hold. Ultimately, for reasons that still remain inexplicable, the FDA lifted that partial clinical hold, which allowed Burzynski to continue to treat patients already on his clinical trials but prevented him from enrolling any new patients (or, as I put it, the FDA really caved). In any case, there hasn’t been much to blog about since the fall, other than noting that the Texas Medical Board (TMB) is trying to do the right thing by going after Burzynski’s license again. There have been a lot of motions and counter-motions, but overall the proceedings have thus far been as exciting as watching paint dry. That s why I haven’t had much interest in covering their ebb and flow, particularly given that I’m not a lawyer, nor am I familiar with Texas law with respect to regulating physicians other than that it is hopelessly slanted in favor of protecting bad physicians more than the public. I’m waiting for the big one, the actual main hearing. Until then, I’m trying to keep my pessimism from depressing me about the long odds the TMB has trying to finally bring down Burzynski.
One thing that’s not going to help Burzynski, contrary to what he apparently thinks, is the recent publication of the results of Hidaeki Tsuda’s clinical trial of antineoplastons in colorectal cancer. Before I discuss the trial, let’s just take a moment to explain what antineoplastons (ANPs) are. I realize that most regular readers are familiar with Burzynski and his antineoplastons, but given that it’s been so long since I’ve discussed him I figured a brief recap is in order. The detailed story is contained in an article I wrote for Skeptical Inquirer entitled Stanislaw Burzynski: Four Decades of an Unproven Cancer Cure. The CliffsNotes version follows. Basically, back in the early 1970s, a Polish expat physician named Stanislaw Burzynski, while working at Baylor, thought he had discovered peptides in the blood and urine that inhibited cancer which he dubbed antineoplastons. His evidence wasn’t the strongest, but it wasn’t outside the realm of possibility that he might have been right. Unfortunately, instead of taking the correct, scientific approach, he bolted Baylor and started treating patients with antineoplastons. By the 1990s, to make a very long, complex story short, he ended up setting up a bunch of clinical trials that were shams, that basically let him administer ANPs as he saw fit. Those were the clinical trials that were put on partial clinical hold and later allowed to proceed, a process detailed in posts showing just how many violations the FDA found in its inspections of the Burzynski Clinic.
In any case, one of the biggest knocks on Burzynski is that he hasn’t published complete results of his clinical trials, although, as I have pointed out, he’s published unconvincing partial results. If there’s one thing, however, that Burzynski apologists like to point out, it’s a clinical trial in Japan run by Hidaeki Tsuda of antineoplastons in colon cancer. It’s a study that featured prominently in Eric Merola’s second propaganda movie about Stanislaw Burzynski. Here’s the segment from the film:
I discussed Dr. Tsuda’s trial in detail on more than one occasion, most notably in my discussion of Eric Merola’s second movie about Stanislaw Burzynski. Hilariously, after the movie, Merola complained about how Tsuda’s trial was rejected by Lancet Oncology. Of course, I wasn’t surprised by this and, in fact, discussed what likely really happened, which, contrary to Merola’s claims, was not that Tsuda’s work was being “suppressed.” (I also couldn’t help but mock Merola for whining about what happens to pretty much every scientist, namely having papers rejected.) Interestingly, another revelation that Merola mentioned was that Tsuda hired a ghostwriter to write the actual manuscript.
So where did Tsuda finally publish his work? Oddly enough, he published it in PLoS ONE. I must admit, I wouldn’t have predicted that journal, given that it’s not exactly known as a journal that publishes cutting edge clinical trials. In fact, although it might be confirmation bias on my part to say so, every clinical trial I recall seeing published in PLoS ONE has been—shall we say?—not particularly good. This one is no exception.
The first thing that struck me about this clinical trial is that it is a negative clinical trial. As much as Tsuda’s group tries to paint it as a positive clinical trial, it is not. Let’s just put it this way. The trial failed to find any effect of antineoplastons on overall survival (OS) or relapse-free survival. That’s a negative trial in any oncologist’s book, regardless of other findings.
But let me back up a bit. Basically, Tsuda’s trial is a randomized clinical trial involving 65 patients with histologically confirmed metastatic colorectal cancer to the liver. Liver metastases from colorectal cancer are one of the exceptions to the rule that metastatic disease from solid tumors can’t be treated for cure in that resecting liver metastases can result in long term survival. In this trial, all of these patients had undergone resection of their metastases or thermal ablation of the metastases and were enrolled between 1998 and 2004 at Kurume University Hospital. These patients were then randomly assigned to receive either 5-FU (a common chemotherapy drug used to treat colorectal cancer) alone by hepatic artery infusion (HAI, control arm) or to receive 5-FU HAI plus systemic ANP therapy, which included intravenous and oral ANPs. One thing that struck me right off the bat is that infusing chemotherapy, particularly only 5-FU, directly into the hepatic artery is already outdated. Given advancements in chemotherapy for colorectal cancer, intravenous chemotherapy using new regimens can do as well or better than infusing 5-FU directly into the hepatic artery (which requires a surgical procedure to insert a catheter attached to a pump and is thus more risky and less desirable than just intravenous chemotherapy).
A curious aspect of this trial is that the investigators specified that this was based on the “number of metastases and presence/ absence of extra-hepatic metastasis at the time of surgery.” To be honest, I’m still not entirely clear what the authors meant by this. Did the investigators choose which group the patient ended up in based on what was found at surgery? Extrahepatic disease (disease outside of the liver) is a bad sign that portends poor prognosis. What I do understand is that the investigators only enrolled patients with an R0 resection, which basically means that after surgery or thermal ablation of liver metastases from colorectal cancer there was no detectable disease left. Thus, at the beginning of the trial, there was no detectable tumor. That was the point and why relapse-free survival was measured.
There are so many problems with this trial. These problems are now much more apparent now that it’s been published. Before, I could only speculate because all I had to go on was Eric Merola’s biased and oncologically ignorant discussions of the trial designed to promote it as evidence that Burzynski’s ANPs are promising antitumor agents. Now, I can look at the published trial results and state unequivocally that I am completely unimpressed, particularly in light of what I know from Eric Merola’s films and other claims made by Burzynski supporters. Yes, this is a randomized clinical trial, but it’s also an open label, non-blinded randomized phase II study (more on that later). That means that the investigators knew who was and was not receiving the experimental treatment. It found no difference in overall survival between the two groups and no difference in relapse-free survival (time to relapse) between the two groups. Nothing. Nada. Zilch. Again, that’s a negative trial. However, it does report a statistically significant difference in cancer-specific survival, with a median survival time of 67 months for the chemotherapy plus ANP group (95%CI 43-not calculated) versus 39 months (95%CI 28-47) (p=0.037) and 5 year CSS rate 60% versus 32% respectively. What does that mean?
At this point, let’s review what these various endpoints mean. Overall survival (OS) is fairly straightforward. It just means the time until the patient dies, regardless of cause. It’s what I like to call a “hard” endpoint, because it’s easy and straightforward. There is no interpretation necessary. A patient is either alive or dead, and investigators know the time from enrollment to the time of death. These are reasons why OS is the “gold standard” for clinical trials testing new cancer drugs. Traditionally, to be approved by the FDA, a cancer drug had to produce a statistically significant improvement in OS. True, as I described discussing the case of Avastin and breast cancer, other measures may be used, but ultimately it comes down to OS. In contrast, relapse-free survival is a measure of the time it takes for cancer to relapse after being seemingly eradicated. In this case, all patients had their cancers eradicated either through surgery to remove their liver metastases or thermal ablation to the point of not having any detectable cancer left; so relapse-free survival in these patients means the time until a detectable cancer relapse is detected, wherever that relapse is.
But what about cancer-specific survival (CSS)? This is a more problematic measure. Basically, according to the SEER Database, it means “probability of surviving cancer in the absence of other causes of death.” To get an idea of what CSS means check out Figure 1 in this article comparing and contrasting the various survival measures used for cancer clinical trials. Basically, CSS ignores locoregional recurrence and censors (does not count) non-cancer-related deaths, deaths from other cancer, treatment-related deaths, and patients lost to followup. It also ignores locoregional recurrence (recurrence in the same organ or the regional lymph nodes), new distant metastases, a second primary of the same cancer type, and a second primary of another cancer. In the same article, there is this graph:
Note how CSS produces the highest survival rate, while disease-free and relapse-free survival rates produce the lowest apparent proportion surviving. In any case, CSS has many problems, including:
In this variant, the event is death specifically from the cancer. Deaths from other causes are not “events” and do not cause the curve to decline. Instead, from the time of death forward, a patient who dies from something else is effectively removed from the data. This decreases the number of patients “at risk” from that point forward but does not cause the curve to decline…Disease specific survival has serious problems. Disease Specific Survival ignores deaths which were (or may have been) due to treatment. For a toxic treatment, disease specific survival could be very different from overall survival and it’s overall survival that counts in the end. Subtle late effects of treatment can make it hard to even know how toxic the treatment actually was, a problem which doesn’t arise when the endpoint is plain survival. Disease specific survival is also known as Cause Specific Survival.
Another problem with CSS is that it is prone to misclassification of cancer-specific deaths, resulting in biased estimates of CSS. In other words, an explicit decision has to be made as to whether a given death observed was due to the cancer. Some deaths will be clearly related to the cancer. In others, the cancer might be a contributory, but not main, factor in the death. This might not be a major problem if the trial were blinded, but the trial was not blinded. The investigators knew who was in each group. It’s impossible to rule out subtle biases leading to the classification of more deaths of patients in the control group as being cancer-specific than in the ANP group. Indeed, it’s hard not to suspect that this is exactly what happened, given not even the whiff of a hint of a statistically significant difference between the ANP and control groups in other endpoints, such as OS and RFS. It’s also hard not to suspect that CSS was not a primary endpoint for the original trial but was added on, post hoc, when it became clear that the differences in OS and RFS were not going to be statistically significantly different. There’s no way of knowing, unfortunately, because the trial was not registered from its outset, but rather in 2013. (In fairness, it wasn’t required to be when it started; the law requiring clinical trial registration came years later.)
Another interesting aspect of this trial is that I now know who is the ghostwriter for Tsuda’s trial. It’s Dr. Malcolm Kendrick, author of The Great Cholesterol Con, which is not a promising start. In any case, Kendrick declares publication of the Tsuda paper as a “victory“:
I was then contacted by someone, who shall currently remain nameless, who told me that a group of Japanese researchers had done work on antineoplastons as adjuvant (add-one) therapy for patients with liver metastases following colorectal cancer. They did not know how, or where, to publish it. So I agreed to look at it, and try and get it published in a peer-reviewed journal.
They were turned down by Lancet Oncology (no surprise), and a couple of other journals. I suggested PLOS (Public Library of Science), which has a high impact and tends to be a bit more open to non-mainstream articles. So we sat down to write, rewrite, edit, alter and adapt.
To be honest, I have never, ever come across so many objections by the peer reviewers. Stuff that was so trivial, so difficult to answer. Re-write, re-write, re-write. Water down the conclusions. I thought by the end of it, nothing would be left, although the most important points did, just about, survive.
Again, as I discussed above, PLoS ONE isn’t really well-equipped to publish clinical trials. Even so, apparently those peer reviewers saw through the hype in the original manuscript immediately (assuming that the first version submitted read anything like what was described by Eric Merola). Good. Interestingly, Adam Jacobs, a UK statistician, comments. Like me, he notes that the primary endpoint (CSS) is an unusual one to use. (It’s worth repeating that CSS is almost never—strike that, never—used as an endpoint in trials intended to be used in applications for FDA approval, for the reasons I’ve discussed above.) He also notes:
Third, and perhaps most importantly (especially in light of my first point), there was no mention of allocation concealment. Do you know if the investigators had access to the randomisation list when recruiting patients? I’m sure I don’t need to explain to you how that would completely invalidate the results of the study if they did.
Yep. Allocation concealment is a procedure that is done in randomized trials to make sure investigators are not aware of what experimental group the patient will be assigned to; i.e., procedures to make sure that neither patients or investigators know what group a given subject will be assigned to. As the World Health Organization (WHO) notes, without allocation concealment, “even properly developed random allocation sequences can be subverted, going on to write:
Within this concealment process, the crucial unbiased nature of randomised controlled trials collides with their most vexing implementation problems. Proper allocation concealment frequently frustrates clinical inclinations, which annoys those who do the trials. Randomised controlled trials are anathema to clinicians. Many involved with trials will be tempted to decipher assignments, which subverts randomisation. For some implementing a trial, deciphering the allocation scheme might frequently become too great an intellectual challenge to resist. Whether their motives indicate innocent or pernicious intents, such tampering undermines the validity of a trial. Indeed, inadequate allocation concealment leads to exaggerated estimates of treatment effect, on average, but with scope for bias in either direction. Trial investigators will be crafty in any potential efforts to decipher the allocation sequence, so trial designers must be just as clever in their design efforts to prevent deciphering.
The methods section of the paper indicates:
Randomization used 50:50 weighting to the two arms and was established by computed macro program in Microsoft Excel 97 (Microsoft Cooperation, Redmond, USA).
Excel? Seriously? Also, how was randomization determined? If anyone had access to the list of assignments beforehand, the process could have been subverted. (See Adam Jacobs’ comments in the comment section below.) Not to diss Excel (too much) as it’s not that horrible a random number generator, but a spreadsheet is not a particularly secure method of determining subject allocation to different arms of the clinical trial.
Here’s an even bigger problem. The trial was also open label, which means it was completely unblinded. The doctors treating the subjects and the researchers analyzing the subjects’ scans (not to mention determining whether a death was due to cancer or another cause) potentially knew which group each subject was in. Knowing the treatment group could easily subtly (or not-so-subtly) influence determinations of whether a death was cancer-related or due to another cause. That’s why, at the very minimum, the investigators determining if relapse had occurred or if a death is related to the subjects’ original cancer or to a different cause. These determinations are not always straightforward. Jacobs is right to emphasize this. Unfortunately, in response to Jacobs’ questions, Kendrick’s answers were—shall we say?—not at all reassuring. In fact, I think Kendrick was downright evasive. For example, even though he bragged about writing the manuscript, whenever questioned about matters like these, Kendrick told Jacobs to contact the investigators. To characterize such a response as “lame” is being generous. Elsewhere, he says things like:
To be frank, I also know that whatever questions are answered, Adam Jacobs (and many others) will always believe it was fraudulent. Any question answered will be followed by another question, and another question, ad infinitum. At some point, as with any trial, there will be imperfections. I know from past experience, that if I make the slightest error, this is leapt upon and used to discredit everything I have to say, on any matter. I spent a year trying to sort out detailed questions about this study. I really, really, do not want to spend another year doing so. Especially when it will make not the slightest difference. Those who disbelieve this study will continue to do so. No matter what. It is the nature of the thing. Please do not confuse weariness with evasiveness – or any other motivation that you may feel is lurking beneath the surface here. Just because someone demands that I answer questions does not mean that I have to do so.
In retrospect I made a tactical error. I should have just said. If you have detailed questions please contact the lead author, or direct questions through the journal. End of.
Funny, for someone who claims to have spend a year editing the paper and “trying to sort out detailed questions about this study,” Kendrick is quick to claim ignorance about a very basic and appropriate question asked by Adam Jacobs. How on earth could he have written the manuscript and not known the answer to this very, very basic question? Is he incompetent? I say yes. And I am not “confusing weariness with evasiveness.” I’m correctly calling out evasiveness.
Meanwhile, Eric Merola is making excuses on Facebook in this hilarious post:
Particularly hilarious to me is the claim by Merola that “the Japanese were forced to ‘water down’ and ‘downplay’ the significance of the studies in exchange for allowing it to be published by the team of oncology peer-reviewers at PLoS ONE (Public Library of Sciences).” Damn those peer reviewers and their pesky insistence on proper statistics! My only thought was, “Dude, welcome to the real world of science! That’s how it’s done! Peer reviewers, when they are doing their job, force authors to stick to only conclusions that can be supported by the data. Having published in PLoS ONE myself a couple of times, I also understand the process a bit from the author’s perspective. Basically, PLoS ONE is very particular about enforcing the journal’s standard that, yes, it will publish pretty much anything (even negative studies) as long as the conclusions are reasonably supported by the science. The moment you go beyond what can be rigorously supported by the evidence in your conclusions and discussion is when the reviewers will stomp on you. I learned that the hard way, and now, apparently, so have Tsuda and Kendrick. Good.
Even more amusing is Merola’s further whine:
PLoS ONE might catch some heat for doing the “right thing” here, they reviewed this manuscript and kept watering it down for over a YEAR before accepting it for publication. The Japanese were forced to say things like “Overall survival was not statistically improved” even though the survival was DOUBLE in the Antineoplastons group. They also had to say “Antineoplastons (A10 Injection and AS2-1) might be useful” – instead of “Is useful”, etc. Baby steps, we guess.
Seldom have I seen such ignorance. OS was not “doubled” if the difference was not statistically significantly different. That’s the definition of “statistically improved,” and Tsuda’s trial didn’t achieve it. As for having the authors say that ANPs “might be useful,” I’d actually say that the reviewers were too easy on Tsuda and Kendrick. The very data presented show that ANPs are not useful as an adjuvant therapy for successfully resected colorectal cancer metastases. Again, this is a negative trial. Indeed, the paper notes that three patients died in the ANP arm from other causes: from pneumonia, from myocardial infarction, from an accidental death. These were not counted in CSS, and it wouldn’t surprise me in the least if they were the reason why OS was not statistically significantly different between the groups, particularly given that the difference in CSS wasn’t impressively different, at least in terms of the p-value (p=0.037).
Poor Mr. Merola. Poor Dr. Kendrick. Poor Dr. Tsuda. They hitched their wagon to Stanislaw Burzynski’s ANPs. Now they can’t unhitch it. Embarrassment is theirs, as well it should be.