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Dear Dr Landgren (author) / Dr Hallstrom (author) / Ms Knight (Editor: Acupuncture in Medicine) / Dr Godlee (Editor-in-Chief of The BMJ)
I am requesting that you withdraw the publication “Effect of minimal acupuncture for infantile colic: a multicentre, three-armed, single-blind, randomised controlled trial (ACU-COL)”. The data as presented shows that across the three trial groups A, B and control group C, there was a large reduction in colic across the trial period and that the largest absolute reduction in the amount of colicky crying was largest in the control group. The trial data as presented does not support the authors stated conclusion that acupuncture reduces crying in infants with colic.
There are obvious causes for concern, including:
The blinding of parents was inadequate. Rather than providing comfort, the authors statement “Nonetheless, among parents of infants who received acupuncture, the percentage of those who believed that the infant had received acupuncture increased at the later visits. This probably reflects the fact that infants receiving acupuncture were deriving greater benefit from treatment” reveals their bias and careless attitude. The data as presented shows that the absolute level of benefit from the treatment was much the same across the Groups so another explanation is required i.e. the parents knew their child was part of the non-control group, or perhaps that parents of children that improved ascribed this to acupunctu...
The blinding of parents was inadequate. Rather than providing comfort, the authors statement “Nonetheless, among parents of infants who received acupuncture, the percentage of those who believed that the infant had received acupuncture increased at the later visits. This probably reflects the fact that infants receiving acupuncture were deriving greater benefit from treatment” reveals their bias and careless attitude. The data as presented shows that the absolute level of benefit from the treatment was much the same across the Groups so another explanation is required i.e. the parents knew their child was part of the non-control group, or perhaps that parents of children that improved ascribed this to acupuncture (whether in the non-control or control group). Analysis of the raw data would easily resolve this question. As the parents are reporting the effectiveness, or otherwise, of the intervention the fact that they were not adequately blinded completely invalidates the study.
The researchers did not acknowledge that the control group, Group C had much greater levels of baseline ‘Colicky Crying’, with this being about 55% higher than Group A and 20% higher than Group B. This implies the study’s sample size was too small, something that the authors acknowledge but gloss over. Again, an insufficient sample size invalidates the study.
Dear Dr Landgren (author) / Dr Hallstrom (author) / Ms Knight
(Editor: Acupuncture in Medicine) / Dr Godlee (Editor-in-Chief of The BMJ)
I am writing to you with great concern and disappointment with
regards to 1) the original article published, online, on the 16 January
2017 (Landgren and Hallstr?m, 2017 ) and, 2) the credibility of the
Acupuncture in Medicine Journal collectively.
I wish to share...
I wish to share the following comments with the editors of both the
Acupuncture in Medicine Journal and the British Medical Journal to raise
awareness of the poor science which has passed publication into a BMJ
Journal. The following is directed toward Dr Landgren and Dr Hallstr?m:
From the offset, a small sample size was noted. ~49 infants were
included in each of the three groups (n=147), including the control (the
nature of which, was not very clear). Only 144 infants were included in
the follow-up. As a result, it is reasonable to assume, from the offset,
that nothing will be conclusively indicated by this trial (despite the
best efforts of the authors). It is further noted, within the discussion,
that "the majority of infants in this cohort did not have colic". These
details alone set off alarm bells and is indicative of a very questionable
The blinding does not stand up to scrutiny. Table 5 shows a clear
difference between parents in groups A & B who guessed correctly, with
regards to guessing whether their child had received acupuncture, than
those in the control group (C). If this had been a robustly blinded trail,
these figures should have been close to equal. Unbelievably, the authors
state informally, "This probably reflects the fact that infants receiving
acupuncture were deriving greater benefit from treatment." - this is an
entirely unsubstantiated claim. It is just as reasonable to suggest that
this was a result of the parents noticing marks on the infant's skin from
the acupuncture needles.
Furthermore, a growing evidence base suggests that the ingestion of
cow's milk is a cause of infantile colic [2,3], and, breastfed infants are
less susceptible to the latter [4,5]. I am curious to know whether more
breastfed infants were found within the acupuncture group, than that of
the control group, as a result of random allocation or careful selection.
Why was this not discussed in the paper?
Although it appears that there was a substantial attempt made to
reduce bias within the methodology of this study, this standard was not
maintained throughout the entirety of the trial. A decision was made,
posthoc, to merge the two acupuncture groups together as one data set. Was
this decision made after it was noted that no significant results could be
identified, without this intervention?
The most troubling aspect of this paper was the statistical analysis
of the data. It is shameful that, between the two authors, the following
poor practices were not noted:
Firstly, one of the most astounding observations is found in Table 1,
which states, "P-values representing a statistical tendency towards
significance (p=0.051-0.1) are italicised." Why were these figures
highlighted, they represent results which are not statistically
It is also accepted within the scientific community that setting a P
value of 0.05 is poor practice. Results close to this value (as in the
'significant results' found in this paper) are shown to have a ~30%
likelihood of existing as false positives, whereas, that percentage
decreases to ~1.8% when a P value of 0.001 is employed. None of the
results in this paper come even close to the latter. A variety of
different P values can be identified within the results of this article.
Of these results, only three were found to be (slightly) below P = 0.05.
It is also not surprising that after the number of comparisons performed
by the authors there were some 'significant' results found - again,
increasing the probability of false positives occurring.
To the editors, it is astonishing and greatly disappointing that this
paper made it into one of the British Medical Journal collections. I hope
that your response will include shared disappointment in the author's use
of such sub-standard practices - both scientifically and statistically.
The article leads me to raise significant concern toward the
credibility of the 'Acupuncture in Medicine' Journal. Why is it, that
after thousands of studies, which has failed to identify any reliable
evidence to suggest acupuncture is an effective treatment, does the BMJ
continue such a publication? Is this not the time to cease continuation of
the pseudoscientific journal?
I hope that the Editor-in-Chief, a vocal critic of "corruption of the
scientific process", and an advocate for the rigorous application of
scientific method, will take action to review the Acupuncture in Medicine
Journal. At the very least, I hope that the current editor of the journal
will ensure a greater level of scrutiny is applied before publications are
accepted in the future.
 Landgren, K. and Hallstr?m, I. (2017) 'Effect of minimal
acupuncture for infantile colic: A multicentre, three-armed, single-blind,
randomised controlled trial (ACU-COL)', Acupuncture in Medicine, (0), pp.
1-9. doi: 10.1136/acupmed-2016-011208.
 Estep, D. and Kulczycki, A. (2000) 'Treatment of infant colic
with amino acid-based infant formula: A preliminary study', Acta
paediatrica (Oslo, Norway : 1992)., 89(1), pp. 22-7.
 Hill, D. and Hosking, C. (2000) 'Infantile colic and food
hypersensitivity', Journal of pediatric gastroenterology and nutrition.,
30, pp. S67-S76.
 Reijneveld, S., Brugman, E. and Hirasing, R. (2000) 'Infantile
colic: Maternal smoking as potential risk factor', Archives of disease in
childhood., 83(4), pp. 302-303.
 Howard, C., Lanphear, N., Lanphear, B., Eberly, S. and Lawrence,
R. (2007) 'Parental responses to infant crying and colic: The effect on
breastfeeding duration', Breastfeeding medicine : the official journal of
the Academy of Breastfeeding Medicine., 1(3), pp. 146-155.