PLOS One seems to have done it again! I wrote a few days ago about how the peer review system at PLOS One seemed to give a free pass to acupuncture studies, when it came to seeking rigorous experimental evidence in support of the claims presented in the paper. I had shared the post via Twitter, and in response, someone from PLOS One had replied:

Well… The day after this reply came, on July 31, 2015, PLOS One published another acupuncture study, in which the hypothesis is that acupuncture along with low-frequency electrical stimulation enhances muscle regeneration, and thereby shows benefit in diabetic myopathy. Oddly (not to mention, rather shockingly), the published study appears to lack the most obvious control for the treatment regimen tested. Allow me to elaborate.

For a quick background, chronic diabetes due to insulin deficiency and/or insulin resistance leads to diabetic myopathy, a clinical condition marked by reduction in skeletal muscle size and strength, with resultant muscle weakness, as well as other metabolic disorders. Stimulation of muscle regeneration with medication and exercise is a key step in combating diabetic myopathy. In this study, experimental mice were made diabetic via injection of a substance called Streptozotocin (which attacks insulin-producing cells in the pancreas, thereby leading to hyperglycemia and eventually diabetes), and was treated with a specialized electro-acupuncture technique called Acu-LFES (Acupuncture plus Low-Frequency Electrical Stimulation), in which low frequency (20Hz) electric current in a low amount (consistent 1 milli-ampere pulses) was delivered to two so-called acu-points close to the knee joints of these mice.

I have earlier voiced my severe reservations with using rodent models in acupuncture studies, especially about localization of acu-points in rats and mice, and the relevance of the concept of Qi, the mystical energy, or the de-qi sensation, which is used subjectively in human patients to guide acupuncture therapy. In addition, the use of the newfangled modality of electro-acupuncture is especially problematic and requires meaningful experimental controls to make any valid conclusion – as I pointed out in this post and this one, critiquing two published studies.

I am bothered by several small methodological and analytical issues in the PLOS One paper – Su et al. – under discussion. Mice were randomized to four groups, control, Acu-LFES, diabetes and diabetes/Acu-LFES. The authors didn’t define what they meant by ‘control’ in the methods; I assume these were non-diabetic, non-treated mice, for whom the diabetic, non-treated mice were a suitable control. The muscles used in the investigation were lower leg muscles, gastrocnemius (outer calf muscle), soleus (calf muscle lying beneath gastrocnemius), and EDL (extensor digitorum longus; muscle connected to four lesser toes) muscle – which stands to reason, given that their acu-points were around the knee. However,

  • Figure 1 uses only the EDL muscle to show that diabetes reduces the muscle fiber cross-sectional area (measure of muscle size), and that Acu-FLES increases it regardless of the diabetes status. Acu-FLES action does not seem to be specific to diabetes. Is this observation generalizable to the gastrocnemius and the soleus? The data, as presented, don’t say. The frequency distribution does seem to show that only muscles with an intermediate area (7-16 µm) are somewhat reduced in number by diabetes. What is the physiological relevance of this observation, especially in respect of the use of Acu-FLES?
  • Both by mRNA transcripts (figure 2) and Western Blots (expressed protein, figure 3), four muscle-associated markers – Pax7, myoD, myogenin and eMyHC – as well as four markers of muscle protein synthesis (figure 5) were lowered in diabetes (not surprising, well established) compared to healthy mice, and Acu-FLES increased them both in presence or absence of diabetes. Similar observations were made with protein metabolism related proteins (figure 6) and cell differentiation associated non-coding microRNAs (figure 8). None of these, again, points to any Acu-FLES function specific to diabetes, and therefore, the causal agency implied in the captions of figures 3 (“Acu-LFES counteracts…“), 5 and 6 (“Acu-LFES improve…“), and 8 (“Acu-LFES increases…“) seems a bit of an overreach.
  • Both IGF-1 mRNA and protein are lowered in diabetes and increased by Acu-LFES regardless of diabetes (figure 7). Given the small magnitude of difference (even if statistically significant) between the control and diabetic group, it is hard to understand the physiological relevance of this observation. Is the upregulation of IGF-1 expression a generally beneficial effect of Acu-LFES, or does it confer some special benefit in diabetes? IGF-1 does have insulin-like activity, but it also has anabolic effect in adults, and is known to be associated with the risk of some cancers. The effects of non-specific stimulation of IGF-1 are not established.
  • Besides, the mRNA and proteins were measured in combined gastrocnemius and EDL muscle lysates, curiously omitting the soleus which they have used for other tests. Therefore, I am not sure of the physiological relevance of this particular observation.
  • There is no difference in migration of satellite cells (adult skeletal muscle stem cells, which help heal injured muscles) between control and diabetic mice as seen with EDL muscles (figure 4). Against that backdrop, what is the point and/or physiological relevance of application of Acu-FLES, which increase satellite cell migration regardless of diabetic status (and may even be indicative of muscle injury due to the electrical stimulation)?

In the Introduction, the authors cite their previous work, where they performed very similar set of experiments in a chronic kidney disease mouse model, and came up with very similar conclusions in that model. So, this is additional corroboration that the effects of Acu-LFES, if any, are extremely non-specific in respect of the condition they purport to treat.

And I admit, I was initially flummoxed by the Table 2. The table header proclaims: Muscle function was increased by LFES. Looking at the table, the muscle grip metrics in all four groups at baseline (before Acu-LFES) are very similar as expected, but the values change in the ‘after Acu-LFES’ column. The way the table is laid out makes it seem that even the diabetes only group received Acu-LFES treatment!

But none of these are my main concerns with this paper – the inexplicable lack of the most obvious control. Where are the data/comparisons between Acu-LFES and plain LFES at random places as control for the electrical stimulation procedure? In absence of this control, how can ANY of the presented observations be said to have anything to do with acupuncture? And if acupuncture were to be responsible for the observed effects, why isn’t there a sham acupuncture control to tease that effect out?

I hope I am getting the importance of this point across. For the electrical stimulation via the acupuncture needles, the needles were placed in two acu-points (Yang Ling Quan, GB34; Zu san li, ST36) which happen to be close to two nerves, the superficial fibular nerve and deep fibular nerve. Given the electrophysiology of muscles and nerves, it is not at all surprising that stimulating either with electrical current will lead to physiological effects. For instance, transcutaneous electrical nerve stimulation, TENS, is a modality which works on those basic principles and shows analgesic effect, even if the mechanistic explanations and evidence for its efficacy are still emerging, and the observed effects may be somewhat non-specific. Similarly, electrical muscle or neuromuscular stimulations have resulted in changes in oxidative enzyme activity, skeletal muscle fiber type and size, even if the heterogeneity of reported studies and study quality made drawing a conclusion difficult. The point is, these electrical stimulation modalities did not need any Eastern mystical mumbo-jumbo, Qi and whatnot, to launch into these investigations.

It is not possible to answer these questions about the specific effect of any acupuncture modality without using proper controls in the studies. So… How is it possible that none of the peer reviewers or the assigned editor at PLOS One caught the methodological and analytical lacuna in this published study?

This is, of course, not the first time I raised concerns an acupuncture study published in PLOS One; I chronicles my concerns in a blog post, and also communicated with the authors via the Readers’ Comments section at the PLOS One site; the senior author responded, but as I have outlined, the reply was not satisfactory by a long shot.

This is the beauty of Tooth Fairy Science, an apt term coined by physician/author Harriet Hall, to describe in depth research on a hypothesis whose fundamental proposition is utterly implausible, built upon a phenomenon that is nonexistent. This study has a strong hypothesis, excellent and consistently-performing animal model, the ability to measure functional correlates (muscle grip function in this case) as well as cellular (quantification of IGF-1 in muscle) and molecular correlates (expression levels of muscle-associated markers and transcription factors), and the use of various immunoassays to help identification and localization of specific proteins. All highly science-y. Strangely, no acupuncture-enthusiast, including those scientists who spend time, energy, and money working on it, is asking the most fundamental questions:

  • Where is the evidence for two most intrinsic assumptions in acupuncture – the flow of Qi, and the anatomical localization of the acu-points?
  • Where is that first study unambiguously showing acupuncture works as claimed, and explaining exactly how it works in the body?
  • Absent such evidence, is it plausible that acupuncture can lead to any specific physiological effect, including those claimed in various studies?