Homeopathy ‘research’: scienciness sans science – Part Deux (paper review)

While contemplating the scienciness of homeopathy research and the time, money and effort wasted by misguided homeopathy researchers, I recently came across a paper which represents one such effort; it was published in the Journal of Analytical Methods in Chemistry in 2012, written by two Indian authors, one from the prestigious Indian Institute of Technology in Kharagpur, West Bengal, and the other from a medical college associated with a local district hospital. Intrigued by the title claim of “Medicinally Active Ingredient in Ultradiluted Digitalis purpurea”, I decided to delve in.

In the abstract, the authors summarized with remarkable clarity the problems that modern medicine has with such faith-based SAD (“Serially Agitated and Diluted”) type of drugs. They wrote: (I have re-arranged their sentences as points)

• The scientific viewpoint attached to the centuries-old therapy with SAD drugs, as in homeopathy, remained doubtful for want of appropriate research and insufficient evidence base.
• The conflicting points related to SAD drug mostly related to
  • the level of concentrations/dilutions,
  • use of drug in contradictory clinical conditions compared to the modern system of medicine,
  • identification of medicinally active ingredient in concentrations and dilutions used in commercially available SAD drugs, and
  • lack of laboratory-based pharmacological data vis-à-vis modern medicine.
• Modus operandi of SAD drug is also unknown.

However, the authors claimed that they addressed some of these issues using an analytical study with a commercially purchased SAD drug, Digitalis purpurea (NOTE 1: Not to be confused with the actual Foxglove plant, Digitalis purpurea, whose extracts contain the potent cardio-specific glycoside Digoxin/Digitalis; NOTE 2: Authors have chosen to deliberately blur this distinction by repeatedly talking about Digoxin/Digitalis, bioavailability and toxicity in the introduction). They analyzed various concentrations of the purchased SAD Digitalis using cyclic voltammetry, emission spectroscopy, and UV-VIS spectroscopy.

The SAD Digitalis was prepared by making a saturated extract in approximately 90% ethanol (in distilled water), which they refer to as ‘θ’; NOTE 3: The method of extraction and chemical equivalents of ‘saturation’ are unclear; the extract was made, I am guessing, by dissolving powdered Foxglove leaves. This extract was serially diluted 100-fold (remember, ‘C’ dilutions) in the same diluent 6 times, achieving a 6C dilution (what the authors refer to as ‘potency’). In mathematical terms, this is a million-million dilution, to the order of 10^-12. Important point to note is that if they had started with 1 mole of the substance, this 10^-12 dilution would actually retain molecules of the substance in solution, i.e. this is not one of those “super-Avogadro” dilutions favored by homeopaths. Whether this particular solution would contain measurable amounts of their analyte of choice or not is unclear, because the starting quantity, or indeed, the analyte(s) they sought to detect, were not mentioned in the text (apart from a vague mention of “Digitalis purpurea (DP), Digoxin, and/or Digoxin-like substance“). Along with θ and 6C, they procured 30C and 200C dilutions also of SAD Digitalis from a local homeopathic pharmacy.

Their positive control and comparison base was commercially purchased Digoxin at 250 mg/L, for which the absorption maximum was 255nm (or 251nm, based on their earlier study) and emission maximum, 318 nm. 6, 30 and 200C dilutions of SAD DP each showed dual emission peaks at 357 and 374 nm, with variable intensities. Several things are not clear in the emission studies:

• Why 255 nm was used for excitation. Depending upon the substance, different excitation wavelength gives rise to different emission intensities. For example, with 256 nm excitation, a 60% ethanol solution in water emits at 310 and 415 nm, but at other excitation wavelengths the intensities vary non-linearly. At 268 nm excitation (absorption maxima for ethanol in water), a 90% ethanol in water emits at 310 and 407 nm. It is possible that for other substances purported to be in the dilutions, the excitation maxima are different.
• Why the fluorescence intensity of 6C was intermediate to that of 30C (higher) and 200C (lower).
• Why the 250 mg/L Digoxin had a much lower intensity compared to the diluted extracts, but it is impossible to draw a conclusion from this because the SAD Digitalis amounts were not chemically defined, and the intensity values were not normalized at the peak maxima.
• Why the authors chose not to run/show a negative control, in form of the diluent, 91.4% ethanol in water, through their spectroscopic tests. This is especially important; it has long been shown [Cf. Ying et al., 2007, Chinese Physics, 16(5):1300-7] that fluorescence emission spectra of ethanol in water differ from those of ethanol or water alone because together they may form cluster molecules via hydrogen bonding. It would have been revealing to know how the ‘super avogadro’ dilutions performed vis-à-vis the diluent.

The authors took recourse to a hand-waving explanation, stating: “Since the medicinally active ingredients in serial dilution of drug are not detectable by the common analytical methods in vogue, the results cannot be compared with usual standard methodologies.” Most emphatically, they did not unambiguously show the presence of “medicinally active ingredients” in the serial dilutions, especially since the exact components present in the θ DP and their relative proportions are not known; in fact, attempting to explain the odd non-linear differences in emission maxima at 318nm, the authors have indicated a possible “interference caused by other inclusions in the samples“. This last bit is particularly important since the authors didn’t mention checking for the presence of impurities in the commercially purchased Digitalis preparations. From previous experience, we know that unaccounted for presence of impurities in this type of physical measurements can significantly alter the observations and analysis.

The other set of studies the authors performed were cyclic voltammetry, a technique used to study electrochemical properties of analytes in solution. In chemistry, this technique is often used to study redox processes (involving oxidation-reduction reactions), such as presence and stability of the intermediates and products of such reactions, and reaction kinetics. Important to note is that in the paper under discussion, the authors chose to study none of these – opting instead to show simple redox potentials of the solutions, which allows no unambiguous conclusion about the purported presence of any substance in the SAD drugs, nor can it make any statement about the purported “medicinal activity” of the SAD drug. Using cyclic voltammetry, concentration of an unknown solution can be determined against a standard curve of current vs. concentration, since concentration is proportional to current in a reversible system; however, the authors made no such attempt at quantification.

What I found even more striking is this: in a figure with six voltammograms (Figure 3), the authors sought to show that “cyclic voltammograms indicate the presence of the peak for Digoxin (purest medicinal derivative of Digitalis purpurea) at the same level as that of serially ultradiluted drugs. This indicates the presence of Digoxin-like substance in the ultradiluted samples of the drug.” To understand this remarkable claim better, I took the figure 3 and superimposed all the panels together, differentiating each curve by a separate color, and retaining the exact scaling that the authors have used. What I came up with was quite revealing.

Image: composite of all six panels of figure 3 of paper under discussion: J Anal Methods Chem, 2012; doi:10.1155/2012/109058.

The finds from this exercise are somewhat interesting.

• Pure digoxin had the highest peak potentials as expected.
• DP6 (Green: the 6C dilution, which still retains some of the original ingredients) understandably showed a lower peak at the same voltage (~0.35 volts).
• DP30 (blue: 30C) and DP200 (red: 200C) show still lower peaks at ~0.35 volts, which if anything is evidence of dilution of the digoxin component in these dilutions.
• Interestingly, at 0.35 volts, DP30 is actually a lower peak than 91.4% ethanol/water; DP200 appears to be slightly higher than ethanol, but then, I don’t know how many times these observations were repeated to ensure fidelity and reproducibility.
• At the other peak at ~0.25 volts, all dilutions are virtually identical to ethanol, which is not unexpected.
• DPQ (Orange: the θ preparation) had a different second peak, at ~0.4 volts. This may be due to the presence of many other substances in it. However, interestingly, the peak height was the lowest, even lower than the dilutions. It is difficult to interpret what this may mean. And the authors certainly haven’t attempted any explanation.

The first line of the abstract of this paper had proclaimed, with no trace of irony, that SAD drugs “available commercially are in use with great faith because of the astonishing results they produce“. I don’t know about others, but I use my medicines not because I have ‘faith’ in them, but because they have been empirically, rigorously tested and demonstrated to have specific effects on the physiological system, and they work regardless of whether I have faith in them or not. Do SAD drugs, then, require faith in order to be useful? Because clearly, the authors – despite their tall claims of “medicinally active ingredients” in these highly diluted preparations – have provided neither good evidence of presence of at least one active substance in them, nor support for the claim of medicinal activity. Their stated conclusion at the end: “Fluorescence spectroscopy and cyclic voltametry both can be used to identify Digitalis purpurea and its derivatives, in commercially available serially ultradiluted solutions.” – is grossly wrong.

Therefore, a related but very important question: How did this paper get through peer review? The journal (Journal of Analytical Methods in Chemistry), published by Hindawi, is an Open Access journal with an impact factor of 0.565. The poor quality of this paper is at par with the “scienciness sans science” of homeopathy research, but is this another indictment on the peer review system, or the Open Access process?