This morning, I was alerted to the latest homeopathy shenanigan via the Forbes column of Dr. Steven Salzberg. (COI statement: I don’t know Dr. Salzberg personally, but I follow his columns, and he is a faculty member at my institution—albeit in a discipline not directly related to mine.) At the heart of it is yet another bog-standard ridiculous “study” purporting to show “clinical effect” of homeopathy, despite the preponderant evidence that homeopathy does not work. What makes this instance special enough for me to take time out from my over-burdened work schedule? The fact that it was published in Scientific Reports from the—wait for it!—Nature Publishing Group. Yes, THAT Nature.
Homeopaths all over are no doubt rejoicing that these homeopath authors from India managed to pull a fast one on the scientific publishing world, getting their paper past editorial desk and peer review into a journal with Nature’s backing behind it. Homeopaths and all practitioners of various pseudoscientific ‘alternative-medicine’ modalities crave the veneer of science, which affords their quackery a modicum of legitimacy and acceptability in the eyes of themselves and their marks, even as they openly flout the scientific principles in their implausible claims. To the credit of the publishers, they have now tacked on this ADVISORY to the published paper…
01 October 2018 Editors’ Note: Readers are alerted that the conclusions of this paper are subject to criticisms that are being considered by the editors. Appropriate editorial action will be taken once this matter is resolved.
… and one hopes the editors will do the right thing and retract the ‘study’. But the fact that this pablum passed peer review in their journal ought to be a black eye for them and their entire publication process, starting with editorial decision making and peer review.
What is wrong in this paper?
Glad you asked. Some critiques of this paper have already been discussed by Dr. Salzberg and others. While taking a quick look at the paper, I was attracted by two things. First, having grown up in a homeopathy-loving family, I am intimately familiar with the homeopathic preparation Rhus tox, a name given to the extract from the plant Toxicodendron pubescens, a.k.a. “Atlantic poison oak”; homeopathic dilutions of this extract—commonly at 30C (that is, 1 volume in 10 raised to the power of 60 volumes) or 200C (that is, 1 volume in 10 raised to the power of 400 volumes)—are used by homeopaths to ‘treat’ inflammatory joint pains. For comparison, one trillion = 10 raised to the power of 12; and earth contains roughly a total of 3.3 x 1020 gallons, or 1.2 x 1024 milliliters of water, which means 1.2 milliliter (think, about one thimbleful) of a substance dropped in the entire water volume of planet earth makes for a 24X (same as 12C) dilution—still smaller than the scope of homeopathic dilutions. So does such an infinitesimally diluted plant extract have any biochemical or physiological property? As I have explained elsewhere, it is well-nigh impossible.
Note from their methods the actual amounts used: they started with 10 gm of powdered T. pubescens leaves dissolved in 100 mL of 70% Ethanol, in which the organic chemical substances in the leaf would gradually leach out over a week. Exact measurement of those individual chemical substances was not done, but overall the original extract may be considered to be 0.1 g/mL, that is 100 milligram per milliliter. It is difficult to estimate exact quantities without knowing the molecular weights of the component substances, but it is safe to say that by their 100-fold serial dilutions, the eleventh dilution (1E-22) is already in the range of having just a few molecules left, which are gone by the next dilution (1E-23) leaving only the diluent (which they don’t mention in the methods; I guess it might be either 70% ethanol or water). Quick note: 70% ethanol (7 volumes of pure ethyl alcohol mixed with 3 volumes of water) is used in laboratories as a disinfectant, because ethanol dissolves the uncharged (non-polar) components of microbial membranes while water dissolves the charged (polar) components leading to death of microbial cells. This is the reason why the authors have indicated that the final concentration of ethanol in all solutions were <0.1%.
Secondly, when I took a look at the actual results in the paper, certain discrepancies became immediately apparent. But before I get into that, let’s see what the authors have claimed using the tools they had. The phenomenon of pain is associated with excessive production of inflammatory substances, such as chemically highly-reactive ionic oxygen species (ROS) and certain proteins called cytokines/chemokines, by cells under stress. For their in vitro studies, the authors used a primary cancer (glioblastoma) cell called U-87, which is capable of secreting these inflammatory substances in response to certain stimuli, including a bacterial product called LPS. For in vivo studies, they used a rat model where pinching of the sciatic nerve (which starts from the spinal chord and runs behind the thighs and calves into the foot) causes nerve (‘neuropathic’) pain. They claimed that homeopathic Rhus Tox alleviated the pain to an extent similar to that achieved by Gabapentin, a medicine used clinically to treat various type of neuropathic pain. [To me, their choice of comparator in the animal model is a bit iffy, because clinically, Gabapentin appears to be ineffective for sciatic nerve pain. But that is a discussion for another time.]
Discrepancies in the Results?
Figure 1 Panel A: I’m not sure what the Panel A was meant to show. Generally, LPS in microgram quantities induces oxidative stress, mediated by ROS, in cultured cells and causes cell death in cell types tested, such as lung cancer cells. Here the LPS was thousand-fold lower (nanogram levels), used in different cancer cells (U-87) which may react differently to LPS. Without looking at the actual data, it is difficult to make sense of the broad statistical significance shown in this panel (and described in the legend) but it seems unlikely that there is any difference as claimed between, say, no Rhus Tox (bar: control + LPS) and 1E-2 Rhus Tox. What is observed (and expected) is that by the eleventh dilution, there seems to be no difference between the Rhus Tox groups and the untreated control.
Figure 1 Panel B, C, D: This shows the production of two enzymes that protect the cells against oxidative damange via ROS and peroxides, namely Superoxide dismutase (SOD) and Catalase. Again, the results (reduction in measurable SOD by LPS) may be typical of the U-87 cells, or of the relatively transient (20 minute) exposure. In certain rat brain cells (astrocytes), LPS may actually induce one type of SOD (Mn-SOD expression), but not the other type (Cu,Zn-SOD); there is also evidence that LPS may lead to release of cell surface SODs into the medium in a dose dependent manner. In any case, these panels show that in presence of diluted Rhus Tox, there appears to be increased SOD and catalase production, and reduced ROS production.
Two curious things are most important to note here: (a) though some of the doses appear to provide a graded effect, we don’t know if the differences are statistically significant; if they are not, the observations might be merely phenomenology. (b) Curiously, the panels B-D show only upto 1E-08 dilution. This is important because the homeopathic claims extend into the impossible dilutions; in fact, that is the principle of classical homeopathy, potentization (making more powerful) by dilution. Note that with a starting concentration of 100 mg/mL, a 1E-08 dilution will contain 1 nanogram (ng)/mL of the bioactive substances from the leaf extract. The ng levels are very much within the realm of active cellular substances, and CANNOT be considered homeopathic in the classical sense.
Figure 1 Panel E-K: Ignoring the obvious mistake of panel G being identical to panel H, these panels are meant to show the decrease in cells producing ROS. The authors used the technique ‘DCFH-DA’ to measure ROS (including peroxide) production. However, there are some important limitations of the technique, including the fact that DCFH does not directly react with the oxidants to produce the fluorescent product, and fluorescence cannot be used as a direct measure of ROS. In the panels, there are two crucial issues as well: (a) Different quadrant gating (marked by blue boxes) for LPS, H2O2 positive control, and the experimental conditions; usually, that is a no-no for Flow Cytometric analysis (see the composite below). (b) No negative (‘No LPS’) control for ROS from Rhus Tox treatments, which is important because no-LPS control (panel E) appears to have some background ROS-producing cellular signal (FITC-A axis) over what was seen in the Rhus Tox treatment groups.
Figure 2 is also plagued with the same issue of an absence of a no-LPS control for Rhus Tox groups. This is important because of the experimental design: after the short LPS exposure, the cells in the Rhus Tox group were further incubated for 24 hours with the dilutions in plain medium. (It is not clear if the LPS group had plain medium with no treatment for the same time.)
Figure 3 and 4 are meant to show the effects of the experimental nerve injury, which is clear from both the low latency of paw withdrawal from painful stimuli and the slow velocity nerve conduction. However, for the experimental groups, it is usually customary to take a baseline measure for each subject, which is used to normalize the observations for each subject in the groups. This appears to have been omitted in the experimental design; therefore, it is difficult to interpret whether the day-to-day variations in the allodynia responses in different groups are normal biological variations or not. Rhus Tox (1E-12: again, not a homeopathic dose) doesn’t seem to have done much for response to warmth (Panel 3B); the response to cold (Panel 3A) is weird since the Gabapentin appears to have a better-than-normal control response; for all, the difference between normal and sham-surgery response is not adequately explained, which makes the interpretation of the observation murkier.
The major problem I have with the rest of the figures is that there isn’t clarity in the methods with clear controls. The histopathology part doesn’t indicate how many sections were observed in total and how representative the presented observations are. Mostly importantly, whether people making the histopathological diagnoses were blinded to the experimental groups or not is not mentioned—which casts a huge shadow re bias. The neural inflammatory surrogates and cytokines were measured from ‘segments’ of the sciatic nerve to obtain something called ‘10% homogenate’; in the method description, there is no mention of how this was achieved without investigator bias, whether same number of segments from the same location were obtained from all the rats in different groups, and so forth. These are variables that may affect the outcome of the assay, and thereby, its interpretation.
When I started writing this, I was not aware that scientists in Italy had also raised concerns about this study’s observations, and various other serious inconsistencies have also been reported by biologist Enrico Bucci.
Overall, this appears to be a rather unsatisfactory study which does not adequately address many of the hypotheses formulated by the authors. And all of these should have been flagged at the peer review stage; it’s a pity they weren’t. The non-homeopathic dosing used for the study doesn’t support its conclusions about homeopathy; however, as an aficionado of ethnobotany and pharmacognosy, I can think of ONE silver lining. If some of these results indeed stand the test of rigorous examination, then it is possible that one or more pharmacoactive principles present in the leaves of the plant T. pubescens may have anti-nociceptive functions. Properly conducted research in that direction may give us a good and effective pain medication in future, just as artemisinin was once discovered and celebrated. Pandering to homeopathic pseudoscience is not the way to achieve that.
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