To the Editor,
We read with great interest the recent publication by Prager et al in BMJ Evidence-Based Medicine (1) and commend the authors on their important work. The authors characterize blinding practices in point-of-care ultrasound (POCUS) diagnostic accuracy clinical research. The authors evaluated whether the interpreter was blinded to patient clinical information in articles published in Emergency Medicine, Anesthesia, and Critical Care journals from January 2016 to 2020. Among 97 studies, the authors found that the POCUS interpreter was blinded to clinical information in 38.1% of studies, not blinded in 35.1%, and that the blinding practice was not reported in 26.8%. They additionally report that the same person obtained and interpreted images in 74.2% of studies, was different in 14.4%, and was not reported in 11.3%. These results demonstrate significant variability in POCUS research, leading the authors to conclude that to ensure generalizability of future research, the same person should perform and interpret the POCUS scan and not be blinded to clinical information.
The authors are firm in their recommendation and its perceived benefit. We believe, however, that it is short-sighted to uniformly recommend a study design in this rapidly evolving field. The authors (and importantly, future researchers) should carefully weigh the advantages and disadvantages of differing study designs. Both blinding and not blinding to clinical information allow co...
The authors are firm in their recommendation and its perceived benefit. We believe, however, that it is short-sighted to uniformly recommend a study design in this rapidly evolving field. The authors (and importantly, future researchers) should carefully weigh the advantages and disadvantages of differing study designs. Both blinding and not blinding to clinical information allow comprehensive evaluation of POCUS for educational uses, quality improvement, and accurate integration into clinical care. The translational science research spectrum provides a framework, from proof of concept to population level outcomes research (2), among which POCUS research undoubtedly falls. Bias, validity, reliability, reproducibility, and the research question are all important considerations researchers need to consider in developing their study design (3, 4).
We disagree with the author’s assertion that research biases are an intrinsic limitation to POCUS research methodology. Importantly, these biases should not be disregarded by unifying research methodology. As an example, researchers evaluating unstudied POCUS techniques will require a different study design than research evaluating a well-established technique, due to differing research questions; even if the final research outcome is the same.
While Prager et al have highlighted differences in study design and limitations to the performance of meta-analyzes because of significant heterogeneity, we would highly encourage prospective researchers to carefully determine the purpose of their project and to design studies to best answer their question while maximizing scientific rigor. We agree with the author’s that applicability of POCUS research to a generalized clinical setting is optimized by tailoring the study design to real-world application but this is not the sole purpose of ultrasound research which also includes education, monitoring, and quality improvement. Each researcher needs to consider his or her study purpose, and design a study to meet that purpose.
1. Prager R, Wu K, Bachar R, et al. Blinding practices during acute point-of-care ultrasound research: the BLIND-US meta-research study. BMJ Evid Based Med. 2020 Nov 11: bmjebm-2020-111577. doi: 10.1136/bmjebm-2020-111577. Epub ahead of print. PMID: 33177166.
2. Westfall JM, Mold J, Fagnan L. Practice-Based Research— “Blue Highways” on the NIH Roadmap. JAMA. 2007; 297(4): 403–406. doi:10.1001/jama.297.4.403.
3. Stone JC, Glass K, Clark J, et al. A unified framework for bias assessment in clinical research. Int J Evid Based Healthc. 2019 Jun;17(2):106-120. doi: 10.1097/XEB.0000000000000165. PMID: 31094882.
4. Simundić AM. Bias in research. Biochem Med (Zagreb). 2013; 23(1):12-5. doi: 10.11613/bm.2013.003. PMID: 23457761; PMCID: PMC3900086.
It would be helpful if it assessed the standard administration quantitatively and specific frequency utilized in the study ‘s participants , or related studies , At the very least - providing a link to the exact dosing used in this study as a reference point would be beneficial .
Drs Clure and Lazorwitz have misunderstood and misinterpreted the Yellow Card data that we adduced to test the null hypothesis that there is no interaction of antibiotics with hormonal contraceptives. Here we reply to their specific comments.
“The medications in each group are not equivalent and bias the sample” We chose a wide range of medicines in order to minimize this. Clure and Lazorwitz have selected only two examples each from the group of nine control drugs and the group of nine non-enzyme-inducing antibiotics, and assert that the age distribution favours older women in the control group. However, they ignore the fact that the same could be asserted of the enzyme-inducing drugs, some of which are more likely to be used in older women, but had an even bigger effect than the antibiotics.
“The rates of unintended pregnancy reported … are much lower than expected in general users of oral contraception” This is an important misunderstanding, which we sought to obviate in the paper, by making it clear that the data do not allow calculation of the absolute rates of unintended pregnancies. That is because the reported rates are not rates of unintended pregnancies in women taking hormonal contraceptives, but the frequencies of reports of unintended pregnancies as a proportion of all reports of suspected adverse reactions. It is the ratios of frequencies that are important. In other words, whatever the baseline risk is, the risk is 13 times higher with enzyme i...
“The rates of unintended pregnancy reported … are much lower than expected in general users of oral contraception” This is an important misunderstanding, which we sought to obviate in the paper, by making it clear that the data do not allow calculation of the absolute rates of unintended pregnancies. That is because the reported rates are not rates of unintended pregnancies in women taking hormonal contraceptives, but the frequencies of reports of unintended pregnancies as a proportion of all reports of suspected adverse reactions. It is the ratios of frequencies that are important. In other words, whatever the baseline risk is, the risk is 13 times higher with enzyme inducers and seven times higher with non-enzyme inducing antibiotics. Because of the possibility of reporting bias the true ratios are probably lower, but unlikely to approach one, in view of the positive control results.
We included a group of enzyme-inducing drugs as a positive control, because it is known that there is an increased risk of an unintended pregnancy if a woman taking a hormonal contraceptive also takes an enzyme-inducing drug. Thus, the Yellow Card data confirm the signal; this shows that analysis of the database is capable of revealing a known interaction. We also included fetal malformations as an outcome, since some of the enzyme-inducing drugs are known to be teratogenic. Again, the database revealed the known signal, even though not all of the enzyme inducers have been associated with teratogenicity, and the size of the signal associated with those that have is therefore probably greater than the data suggest. Further support for the usefulness of the database comes from the inclusion of negative control outcomes (cardiac arrhythmias and headache), which would not be expected to yield a signal, and which did not.
“Pharmacologically, the progestin component of combined oral contraceptives provides the main contraceptive effect” The estrogenic component in a formulation also contributes to inhibition of ovulation, by an action on FSH. This point in fact strengthens the observation that this interaction is likely to be experienced by only a subset of women, those in whom a perturbation of the amount of unbound estrogen to which they are exposed is enough to make a difference between effective and ineffective contraception.
“it is important to not create false concern” We believe that it is more important that women should not be advised that the interaction does not exist, thus potentially exposing them to the risk of an unintended pregnancy. Women should be informed about the possibility of an interaction and be empowered to decide for themselves what to do about their contraceptive practices during short courses of antibiotics. During longer courses of antibiotics (more than 3–6 weeks), it is likely that the intestinal bacteria become resistant to the effects of commonly used antibiotics  and that the risk of an unintended pregnancy is much less, assuming that the mechanism is mediated by an effect on gut bacteria. However, we have no data to support advice in such cases, and that is a question that could be usefully researched.
We expect that others will find reasons for denying the existence of this interaction. However, UK Summaries of Product Characteristics (“labels”) continue to warn about it [2,3,4] and even those who have not found confirmatory evidence in formal studies have acknowledged, for example, that women “should be advised that this antibiotic/OC controversy exists” .
1. Zlitni, Bishara A, Moss EL, Tkachenko E, Kang JB, Culver RN, Andermann TM, Weng Z, Wood C, Handy C, Ji HP, Batzoglou S, Bhatt AS. Strain-resolved microbiome sequencing reveals mobile elements that drive bacterial competition on a clinical timescale. Genome Med 2020; 12: 50.
2. Flamingo Pharma. Amoxicillin 500 mg capsules. https://www.medicines.org.uk/emc/product/11312/smpc.
3. Intrapharma Laboratories Ltd. Oxytetracycline 250 mg tablets. https://www.medicines.org.uk/emc/product/ 4175/smpc.
4. Aspen. Co-trimoxazole 80/400 mg tablets. https://www.medicines.org.uk/emc/product/ 6999/smpc.
5. Helms SE, Bredle DL, Zajic J, Jarjoura D, Brodell RT, Krishnarao I. Oral contraceptive failure and oral antibiotics. J Am Acad Dermatol 1997; 36(5 Pt 1): 705-10.
Pawlak1 critiqued our challenge to conventional dietary guidelines for people diagnosed with familial hypercholesterolaemia (FH)2. Indeed, his criticism was so incriminatory that he stated our recommendation “constitutes malpractice”. Considering the gravity of his claim, especially as it is levied against co-authors who are mostly MDs, it is important to disclose what we actually recommended, and to point out the flawed evidence Pawlak used to claim that we have committed malpractice.
First, Pawlak misunderstood the purpose of our paper. We did not question “the efficacy of low-saturated fat, low-cholesterol diet to reduce LDL cholesterol”, as he stated. We provided strong support for the hypothesis that factors other than LDL-C, such as smoking, hypercoagulation and hyperinsulinemia, have a potent influence on the incidence of coronary events in FH that dwarfs that of LDL-C3. For example, in our Figure 4 we illustrated the findings of Gaudet et al.4, who demonstrated that FH people without obesity or insulin resistance had no greater rate of coronary heart disease (CHD) than non-FH people. In contrast, obese, insulin-resistant FH people had over 7 times greater incidence of CHD than non-FH people. Moreover, in recent work we have elaborated on the extensive, but largely ignored, literature demonstrating that factors other than LDL-C, such as increased levels of coagulation factors, explain why only a subset of FH individuals develop premature CHD5. Finally, we in...
First, Pawlak misunderstood the purpose of our paper. We did not question “the efficacy of low-saturated fat, low-cholesterol diet to reduce LDL cholesterol”, as he stated. We provided strong support for the hypothesis that factors other than LDL-C, such as smoking, hypercoagulation and hyperinsulinemia, have a potent influence on the incidence of coronary events in FH that dwarfs that of LDL-C3. For example, in our Figure 4 we illustrated the findings of Gaudet et al.4, who demonstrated that FH people without obesity or insulin resistance had no greater rate of coronary heart disease (CHD) than non-FH people. In contrast, obese, insulin-resistant FH people had over 7 times greater incidence of CHD than non-FH people. Moreover, in recent work we have elaborated on the extensive, but largely ignored, literature demonstrating that factors other than LDL-C, such as increased levels of coagulation factors, explain why only a subset of FH individuals develop premature CHD5. Finally, we included in our paper a review of the literature demonstrating that elderly people with the highest levels of LDL-C show either an equal or lower rate of mortality than people with the lowest LDL-C6. Other work, as well, has shown that FH people at 70 years of age have a significantly lower 10 year mortality rate compared to the general population7. Therefore, we find no reason to recommend that FH people reduce their LDL-C levels with diet or medication.
The primary purpose of our paper was to point out that low cholesterol, low saturated fat diets have been recommended to FH individuals for over 80 years, without any evidence of benefit. Indeed, we stated in our paper that diets that are low in fat are therefore high in carbohydrates, which may promote an atherogenic biomarker profile. What we did recommend was that FH individuals with components of the metabolic syndrome, e.g., excess weight, hypertension, hyperinsulinemia or hyperglycemia, would benefit from a diet low in carbohydrates. Support for this recommendation is based in the vast literature on clinical trials utilizing the low carbohydrate diet (LCD), which has shown its effectiveness in improving CHD-sensitive biomarkers, at a level equal to or superior to low fat diets8. The well-established benefits of an LCD in improving CHD-sensitive biomarkers supported our recommendation that a clinical trial should be performed with LCD only in FH individuals with components of the metabolic syndrome or excess hypercoagulation markers.
Second, based on the findings of 3 publications, two of them conducted on non-FH rodents and one in non-FH people, Pawlak claimed that our recommendation of the LCD for FH would “exacerbate atherosclerosis”. It is therefore important to assess whether the findings of these three papers justify his concern that the LCD is inherently atherogenic.
Two studies Pawlak cited were conducted on genetically manipulated mice designed to model human atherosclerosis9 10. Research on a rodent model of a human disease should be scrutinized closely to satisfy criteria in which the methods and biomarker outcomes are comparable to the human condition. These two studies do not satisfy these criteria. The diets of the animals are unlike a typical diet a human would consume, in general, and certainly do not match the diet of someone on an LCD. In the Foo et al.,9 study, the food was composed of sugar (8.4%), corn starch (3.6%), casein protein (45%) and milkfat (43%). This diet has no relevance to human nutrition, with one of numerous flaws being that an LCD is typically composed of 20-25% protein, 60-70% fat and 10-15% carbohydrates. Indeed, a diet that contains more protein than fat is likely to make a person ill. The second study by Kostogrys et al.,10 as well, contained a diet for the rodents with a dietary composition that no human should consume; it contained 52% protein, 12% sugar, 5% corn starch, 21% fat (butter), and the remainder as cellulose and minerals. Confirmation that these findings are unrelated to human research on LCD is that in both studies the mice developed hypertriglyceridemia, an effect that does not happen in people on LCD8. These rodent studies, therefore, have no translational value toward understanding LCD effects on CHD.
Animal research that is more relevant to mechanisms underlying premature CHD in FH individuals is provided by the Watanabe rabbit model of FH, which has high cholesterol, elevated coagulation factors (Factor VIII and fibrinogen) and develops human-like atherosclerosis.11 12 It is of value that the development of atherosclerosis in the Watanable rabbit was prevented by probucol, a medication which also reduces cardiovascular events in FH people.13 Most importantly, probucol reduced coagulation factor levels without lowering their high cholesterol.12
Pawlak cited a 20 year old clinical study that he asserted documented “the progression and the severity of CAD” (coronary artery disease) in people on an LCD. The problems with this cited study are so extensive they could fill a textbook on flawed scientific methods. First, the repeated blood work and cardiac imaging in this year-long intervention study would have had a very high cost, but no funding source was mentioned in the paper. Second, subjects were given dietary guidance, but the study did not include a registered dietician. Third, it is stated that each individual was questioned regarding dietary habits, but there is no record of what the subjects consumed. Specifically, there is no quantification of the categories, macronutrients or amount of food the subjects in the two groups ate. Fourth, there is a vague, unsubstantiated statement that a subset of patients adopted a ‘high-protein diet’, which, in theory, is equivalent to an LCD. However, there is no confirmation as to whether the ‘high-protein diet’ as described by Fleming was an LCD. Fifth, this author published related work with the same dietary program that demonstrated an increase in triglycerides in subjects on a high fat diet. The finding that people on the high fat diet developed hypertriglyceridemia is inconsistent with every other study on LCD effects on triglycerides. Overall, the work by Fleming is flawed at every level of analysis, and his findings have not been replicated by any LCD study.
The fact that Pawlak has depended on three fatally flawed studies to justify his claims that an LCD is harmful provides strong support for our contention that there is no high caliber research that demonstrates the LCD is harmful. A relevant year-long study conducted at Stanford University demonstrated that the LCD was equal or superior to other diets, including a low saturated fat (Ornish) diet, in terms of cardiovascular biomarker risk outcomes.14
Finally, Pawlak praised the effects of a low-fat, vegetarian diet in improving cardiovascular health, citing work by Ornish et al.15 However, the Ornish work was not solely a diet study. It involved an experimental group that was prescribed an intensive lifestyle intervention that included a low fat, vegetarian diet, as well as aerobic exercise sessions, stress management training, smoking cessation, group psychosocial support, and they were told to avoid sugar consumption. Control subjects were given no interventions other than to follow routine advice from their personal physicians. The multi-factorial nature of the intervention group does not permit the conclusion that any one factor, such as diet, was causally related to the outcomes of the study. It should be noted, as well, that despite the intensive lifestyle intervention in the experimental group, there was no difference in hard cardiovascular outcomes, such as the incidence of myocardial infarctions, coronary artery bypass grafts or death, between the two groups.
In conclusion, Pawlak has failed to justify his charge that we have committed malpractice by recommending that FH individuals with components of metabolic syndrome should follow a carbohydrate restricted diet.
1. Pawlak R. Low carbohydrate diets should NOT be recommended for patients with familiar hypercholesterolaemia. BMJ-Evidence Based Medicine 2020.
2. Diamond DM, Alabdulgader AA, de Lorgeril M, et al. Dietary Recommendations for Familial Hypercholesterolaemia: an Evidence-Free Zone. BMJ Evid Based Med 2020.
3. Ravnskov U, de Lorgeril M, Diamond DM, et al. LDL-C does not cause cardiovascular disease: a comprehensive review of the current literature. Expert Rev Clin Pharmacol 2018;11(10):959-70.
4. Gaudet D, Vohl MC, Perron P, et al. Relationships of abdominal obesity and hyperinsulinemia to angiographically assessed coronary artery disease in men with known mutations in the LDL receptor gene. Circulation 1998;97(9):871-77.
5. Ravnskov U, de Lorgeril M, Kendrick M, et al. Inborn coagulation factors are more important cardiovascular risk factors than high LDL-cholesterol in familial hypercholesterolemia. Med Hypotheses 2018;121:60-63.
6. Ravnskov U, Diamond DM, Hama R, et al. Lack of an association or an inverse association between low-density-lipoprotein cholesterol and mortality in the elderly: a systematic review. Bmj Open 2016;6(6).
7. Mundal L, Sarancic M, Ose L, et al. Mortality among patients with familial hypercholesterolemia: a registry-based study in Norway, 1992-2010. J Am Heart Assoc 2014;3(6):e001236.
8. Diamond DM, O'Neill BJ, Volek JS. Low carbohydrate diet: are concerns with saturated fat, lipids, and cardiovascular disease risk justified? Curr Opin Endocrinol Diabetes Obes 2020;27(5):291-300.
9. Foo SY, Heller ER, Wykrzykowska J, et al. Vascular effects of a low-carbohydrate high-protein diet. Proc Natl Acad Sci U S A 2009;106(36):15418-23.
10. Kostogrys RB, Franczyk-Zarow M, Maslak E, et al. Low carbohydrate, high protein diet promotes atherosclerosis in apolipoprotein E/low-density lipoprotein receptor double knockout mice (apoE/LDLR(-/-)). Atherosclerosis 2012;223(2):327-31.
11. Watanabe Y. Serial inbreeding of rabbits with hereditary hyperlipidemia (WHHL-rabbit). Atherosclerosis 1980;36(2):261-8.
12. Mori Y, Wada H, Nagano Y, et al. Hypercoagulable state in the Watanabe heritable hyperlipidemic rabbit, an animal model for the progression of atherosclerosis. Effect of probucol on coagulation. Thromb Haemost 1989;61(1):140-3.
13. Yamashita S, Hbujo H, Arai H, et al. Long-term probucol treatment prevents secondary cardiovascular events: a cohort study of patients with heterozygous familial hypercholesterolemia in Japan. J Atheroscler Thromb 2008;15(6):292-303.
14. Gardner CD, Kiazand A, Alhassan S, et al. Comparison of the Atkins, Zone, Ornish, and LEARN diets for change in weight and related risk factors among overweight premenopausal women. Jama-Journal of the American Medical Association 2007;297(9):969-77.
15. Ornish D, Scherwitz LW, Billings JH, et al. Intensive lifestyle changes for reversal of coronary heart disease. JAMA 1998;280(23):2001-7.
To the editor,
We read the article “Effectiveness of honey for symptomatic relief in upper respiratory tract infections: a systematic review and meta-analysis” with great interest. The need to discover effective remedies for symptomatic relief of upper respiratory tract infections (URTIs), while preventing further antimicrobial resistance developing is indeed paramount. However, after reading the article in detail, we noted a number of discrepancies which we feel must be highlighted and addressed.
Firstly, we believe that the article is misleading, and if read as a lay member of the public, or indeed by a sensationalist news outlet, incorrect and potentially health-threatening conclusions may be drawn and promoted. Firstly, the abstract focuses on positing honey as an alternative to antibiotics for the symptomatic relief of URTIs. The authors highlight that honey possesses antimicrobial properties, with the conclusion of the abstract affirming that it is a “widely available and cheap alternative to antibiotics”. The abstract also concludes that honey improves symptoms in comparison with “usual care”, which, left hitherto unspecified, and paired with the aforementioned focus on a comparison between honey and antibiotics, again augments the misleading introduction to the article. Fundamentally, none of the 14 the studies included within the systematic review compare the use of honey with the use of antibiotics. Focusing so strongly on comparing honey to antib...
Firstly, we believe that the article is misleading, and if read as a lay member of the public, or indeed by a sensationalist news outlet, incorrect and potentially health-threatening conclusions may be drawn and promoted. Firstly, the abstract focuses on positing honey as an alternative to antibiotics for the symptomatic relief of URTIs. The authors highlight that honey possesses antimicrobial properties, with the conclusion of the abstract affirming that it is a “widely available and cheap alternative to antibiotics”. The abstract also concludes that honey improves symptoms in comparison with “usual care”, which, left hitherto unspecified, and paired with the aforementioned focus on a comparison between honey and antibiotics, again augments the misleading introduction to the article. Fundamentally, none of the 14 the studies included within the systematic review compare the use of honey with the use of antibiotics. Focusing so strongly on comparing honey to antibiotics, both within the abstract and throughout the article, with the conclusion stating that authors “would recommend honey as an alternative to antibiotics”, is unjustified, and may have potentially dangerous implications for those misled by the statements.
The statements regarding antibiotics themselves are also both vague and misleading. Authors state that “the use of antibiotics for URTIs is a particular problem, because they are ineffective”, which, as a sweeping statement, is highly inaccurate. The claim that antibiotics are “associated with significant adverse effects in children and adults” is also imprecise and over-generalised, again contributing to the article’s potential to both misinform readers and promote scaremongering. We also feel there should also be more clarity with regards to the age restrictions surrounding the therapeutic recommendations for honey. While the authors briefly mention within their discussion that honey is not commercially safe for those who are allergic and infants under 1 years old, there is no mention of any age limitations within the introduction and conclusion section of this statement being made.
It must be noted that the studies included within the systematic review contain high levels of bias, which limits both the reliability of the results and the conclusions made. For instance, authors utilise the Cochrane risk of bias tool, which states that the overall risk of bias for each article is the lowest favourable assessment of all domains . Therefore, according to Figure 2 of the article, a “Summary of risk of bias assessment for included studies” - for which no key is provided - 9 of the studies are classified as having a ‘high risk’ of bias, with 5 classified as having ‘some concerns’. This is contrary to what is stated in the article; authors claim that two articles were at ‘low risk’ of bias, with the overall risk of bias being ‘moderate’. Authors therefore seem to have assigned a lower level of bias to the studies than classified by the Cochrane risk of bias tool, which, paired with the fact that the majority of the studies included have a high risk of bias, further acts to decrease the reliability of the conclusions made. Additionally, the high level of disparity between the variables within the studies decreases the validity of the conclusions even further. There are over 14 variations of interventions, and 10 variations of comparators, between the 14 studies. This high level of bias and variability amongst the studies included thus renders the findings of the systematic review, and therefore the ability to
judge the efficacy of honey on URTIs, highly limited.
Furthermore, it is important to maintain appropriate antimicrobial stewardship when practicing medicine. However, this article provides little delineation as to what particular organisms honey would be effective against. For instance, not all members of the public will be aware that antibiotics are ineffective against viral infections. Whilst the authors state “the majority of URTI’s are viral, therefore antibiotics would be ineffective” – there is little mention with regards to bacterial, fungal or helminthic organisms – and the vagueness of the statement above could be considered misleading. Having shown this article to persons of a non-medical background, it became obvious that there was a lack of clarity, creating confusion as to whether honey should be used for all organisms, or just viral ones. Additionally, the National Institute of Clinical Excellence (NICE) recommends Phenoxymethylpenicillin or Clarithromycin/Erythromycin for the treatment of patients with suspected bacterial URTIs, who score high enough using the FeverPAIN or Centor score . Readers of this paper may wrongly be given the impression that honey supersedes the use of antibiotics for any infection, and therefore treat themselves or others in their care as such. With some infections, such as streptococcus, having the potential to cause significant morbidity if left untreated by antibiotics , the misinformation within this article could lead to the development of rheumatic fever and cardiac complications later in life.
Ultimately, our aforementioned points; the lack of clarity throughout the article, the bias within each study, and the significant variability between the studies’ variables combine to create a misleading article, with potentially damaging consequences for the lay public. Dangerous decisions could ultimately be made, with our main concern being that people may delay seeking appropriate medical help for a condition for which honey is ultimately not the appropriate treatment; in turn this could increase both morbidity and use of NHS resources. With the propensity for news outlets to grasp for controversial headlines, and promoting them in a further misleading and sensationalist manner, we feel that a more balanced argument needs to be put forward, in order for a responsible message on this interesting, pertinent topic to be conveyed.
1. Chapter 8: Assessing risk of bias in a randomized trial | Cochrane Training. https://training.cochrane.org/handbook/current/chapter-08. Accessed October 2, 2020.
2. Respiratory Tract Infections-Antibiotic Prescribing Prescribing of Antibiotics for Self-Limiting Respiratory Tract Infections in Adults and Children in Primary Care. www.nice.org.uk. Accessed October 2, 2020.
3. Thompson KM, Sterkel AK, McBride JA, Corliss RF. The Shock of Strep: Rapid Deaths Due to Group a Streptococcus. Acad Forensic Pathol. 2018. doi:10.23907/2018.010
The Murphy et al. letter1 is notable for its ad hominem claims, the first of which comes in their introductory remarks. Noting that my review2 reports no conflicts of interest, they make the exaggerated claim that I have “written extensively on the ‘lethality’ of caffeine”. That claim cites one published article, titled “Death by Caffeine”,3 which summarises reports of death by poisoning involving documented cases from coronial and other official public inquiries. As reported in that article, official records in several countries report multiple confirmed cases of death by poisoning due to caffeine. Although relatively rare, such cases have been (and continue to be) reported worldwide. Predicated on the mere fact that I have previously reported findings from official inquiries into caffeine-related harm, the claim by Murphy et al. of “conflict” is perverse. By implication, their reasoning would mean that the reporting of harm from any source (which includes much of the content of medical journals) renders authors (i.e., most medical researchers) evermore vulnerable to bias warranting formal disclosure of conflict of interest in all future reports on the same or related topic. Of course, no such custom or practice exists.
Notably, the assertion of conflict in this instance indicates poor understanding of the matter, a lamentable situation considering the professional identities of Murphy and her 20 co-authors. Conflict of interest arises when a primary interest conf...
Notably, the assertion of conflict in this instance indicates poor understanding of the matter, a lamentable situation considering the professional identities of Murphy and her 20 co-authors. Conflict of interest arises when a primary interest conflicts with a secondary interest.4,5 Examples of healthcare primary interests include researcher interest in producing generalisable knowledge, educator interest in sharing impartial knowledge, and healthcare personnel interest in delivering effective care. The quintessential example of secondary interest requiring disclosure is potential financial gain. However, disclosure is also required in such circumstances as affiliation with a stakeholder where such association could serve a secondary interest even when direct financial reward is not involved. We have no such affiliations, and our studies of caffeine, including caffeine and pregnancy,6 do not generate income.
Echoing sentiments held by O’Connor7 and Fernando,8 Murphy et al. claim that because my article2 is a narrative review, it falls “short of the standards”. In reality, it is common knowledge that all methods of scientific review possess particular advantages and disadvantages. In common with all scientific enterprise (including theoretical and empirical endeavours), each instance of scientific review should be assessed on its merits. The fact that much of the published literature examined in my review is in the form of systematic reviews and meta-analyses contributed to the choice of narrative review in this instance. Given the inconsistency between persistent claims of safety, on one hand, and extensive reports from prior quantitative syntheses of significant caffeine-related negative pregnancy outcomes on the other, there was need for the quantitative literature to be synthesised conceptually by way of “traditional” or narrative review. The claim by Murphy et al. of inherent superior objectivity for one or other review approach over legitimate alternatives reveals poor understanding of review practice and tradition.
Murphy et al. also claim that the articles examined in my review may not be “an unbiased reflection of the literature”. However, the review is transparent with respect to source material, and anyone concerned about selection bias is free to identify additional material. Murphy et al.’s belief that such material exists, despite no attempt by them to identify it, could itself be suggestive of bias. A litany of complaints then follows, wherein Murphy et al. express views contrary to those argued in the review. In particular, while it is (in their words) “clear that caffeine intake is associated with a higher risk of adverse pregnancy outcome”, Murphy et al. nevertheless seem unwilling to consider the implications of that reality. Oddly, they engage in ad hominem generalisations about confounding/misclassification and evidence of causation, when much of the review addresses those very issues in detail.
Under the heading “recommendations” and “lived” experience, Murphy et al. draw attention to concerns about the potential for information such as that reported in the review to cause distress, especially among women who have experienced a negative pregnancy outcome. This is a dilemma of real concern demanding calm and sensitive attention. Murphy et al.’s proselytising does not treat that dilemma with the calmness and sensitively it deserves, nor is the complex multifaceted nature of the dilemma given due consideration. While it is undeniably important that anxiety and guilt be avoided where possible, it is equally important not to withhold inconvenient information, especially information that could assist women in avoiding preventable harm. Thus, it is obviously appropriate to address anxiety or guilt women may feel on receipt of potentially disturbing new information. Likewise, it is important that appropriate support be given in the event of anger and anxiety being triggered when women learn of the failure by relevant authorities to give due prominence to long-held suspicions about caffeine-related harm.
Unfortunately, the contribution of moderate caffeine consumption to negative pregnancy outcomes does not leave an indelible footprint in its wake. Thus, for those who have experienced a negative pregnancy outcome, it is important to stress that caffeine could be but one of a plethora of potential contributing factors. There is simply no basis for making a specific assessment about the possible contribution of caffeine at the level of the individual case. It is equally important, however, to understand that whereas caffeine-related increased risk of harm is small at the level of each individual, that small increased risk when aggregated across populations is demonstrably not trivial,9 as evidenced by the many articles examined in our review.2 Geoffrey Rose, the eminent British epidemiologist, expressed the relevant principle well when he stated, “A population-wide preventive measure [in this instance, avoidance of caffeine during pregnancy] may offer a disappointingly trivial benefit to individuals, but yet its cumulative benefit for the population as a whole can be unexpectedly large” (pp. 102).10
Sadly, Murphy et al. falsely state that the review contains a “claim that 280,000 of the approximately 1 million miscarriages that take place in the USA each year are attributable to maternal caffeine consumption”. The claim appears to be a deliberate misreading of a table in an earlier version of the review. The earlier version (which I decided to amend) included a table (Table 3) predicated on a series of assumptions that included a hypothetical scenario about possible implications were all pregnant women to consume the recommended “safe” level of 200 mg caffeine per day (which the review posited as a purely theoretical, and unlikely, occurrence). However, it was apparent from early reader comment that speculation based on a hypothetical scenario, overtly intended merely to illustrate a point of principle, was potentially confusing and risked diverting some reader attention away from key evidence-based conclusions in the review. Accordingly, I deleted the content describing hypotheticals from the final version. Murphy et al.’s attempt to discredit the review by misreporting material that had been formally withdrawn seems to vindicate the decision to omit that content. However, it is important to note that inclusion or omission of the aforementioned theoretical argument has no bearing whatever on the conclusions, which remain entirely unaltered in both the earlier and amended (i.e., current) version of the manuscript.
Expressing a novel objection, Murphy et al. suggest that the conclusions of the review are “irresponsible” because women are incapable of avoiding caffeine. In that context, it is important to note that caffeine is a psychoactive substance and that repeated exposure leads to physical dependence.11,12 At the same time, it is equally important to understand that the addictive potential of caffeine is less than that of classic drugs of abuse (e.g., alcohol, amphetamines, cocaine, opioids). Indeed, relevant empirical research shows that simple and effective strategies are available to enable those who desire to reduce or eliminate caffeine consuming habits to succeed in so doing.13-15 The terms “avoid” and “eliminate” in this context refer to caffeine beverages (coffee, tea, so-called “energy” drinks, etc.) which account for almost all of the caffeine that is regularly consumed.
Caffeine at considerably lower concentrations is also contained in decaffeinated coffee and tea, hot chocolate, chocolate bars, chocolate confectionaries, and chocolate cake. Combined, those sources account for a trivial proportion of the total caffeine consumed worldwide, and are not the targets of the avoidance advice contained in our review. It is unclear why Murphy et al. prejudge pregnant women as incapable of avoiding caffeine. A more constructive approach would be to promulgate evidence-based findings and invite women to decide for themselves whether to expose their unborn child to a psychoactive drug, albeit one that is currently widely used, or to have, as far as is possible, a drug-free pregnancy.
To repeat key points from the review:2 chronic chemical exposure during pregnancy is always cause for concern; there is undisputed high biological plausibility of harm from caffeine consumed during pregnancy; there is consistent evidence of harm from diverse animal experiments, human observational studies, systematic reviews, and meta-analyses; findings are robust to threats form confounding and misclassification; caffeine has no nutritional benefit for either mother or baby; and persons wishing to reduce or eliminate dietary caffeine can do so successfully when shown how. Those and other realities provide compelling grounds for questioning the soundness of current advice about the reputed safety of “moderate” caffeine consumption during pregnancy.
Finally, while there is no reason to question good intentions, the emotional tone of the Murphy et al. letter and their fervent belief in the correctness of their views (despite current realities as summarised in the preceding paragraph), bear the hallmarks of a common cognitive bias, well-known to social psychology as self-serving bias. Extensive experimentation shows that human decision making is subject to an unintentional and unconscious self-serving bias, wherein reason and judgment are skewed in favour of outcomes in which the individual has a prior stake.16 It is reasonable to assume that most, if not all, of Murphy and her 20 co-authors are habitual caffeine consumers, sharing common features with other consumers, including physical dependence and desire to continue to consume. The self-serving bias therein is likely to encourage resistance to information that challenges habit. Absent of sound argument to reject the challenge, strong emotion and fervent belief typically come to the fore. Such reactions are understandable but regrettable. The public’s stake in women’s health is of a magnitude that calls for calm reflection and preparedness for sober engagement with the evidence concerning caffeine-related negative pregnancy outcomes.
1. Murphy C, Brown T, Trickey, H, et al. It remains unclear whether caffeine causes adverse pregnancy outcomes; but naive policy recommendations could cause harm. Evid Based Med 2020. Available: https://ebm.bmj.com/content/early/2020/09/01/bmjebm-2020-111432.responses.
2. James E. Maternal caffeine consumption and pregnancy outcomes: A narrative review with implications for advice to mothers and mothers-to-be. Evid Based Med 2020;25. Available: doi.org/10.1136/bmjebm-2020-111432.
3. James JE. Death by caffeine: How many caffeine-related fatalities and near–misses must there be before we regulate? J Caffeine Res 2012;2:149-152.
4. Relman AS. Dealing with conflicts of interest. N Engl J Med 1984;310:1182-3.
5. James JE. Disclosing conflict of interest does not mitigate healthcare bias and harm: It is time to sever industry ties. Eur J Clin Invest 2020;50, doi.org/10.1111/eci.13344.
6. James JE, Paull I. Caffeine and human reproduction. Rev Environ Health 1985;5:151–67.
7. James JE. Caffeine and Pregnancy: Bias? Is the pot calling the kettle black? Reply to O'Connor. Evid Based Med 2020;25.
8. James JE. Caffeine and pregnancy: Don’t shoot the messenger, please. Reply to Fernando. Evid Based Med 2020;25.
9. James JE. The health of populations. London: Elsevier-Academic Press, 2016
10. Rose G. The strategy of preventive medicine. Oxford, UK: Oxford University Press, 1992.
11. Griffiths RR, Juliano LM, Chausmer AL. Caffeine: pharmacology and clinical effects. In: Graham AW, Schultz TK, Mayo- Smith MF, Ries RK, Wilford BB (eds) Principles of addiction medicine, 3rd edn. (pp 134–193). Chevy Chase, MD: American Society of Addiction Medicine, 2003.
12. James JE, Rogers PJ. Effects of caffeine on performance and mood: Withdrawal reversal is the most plausible explanation. Psychopharmacol 2005;182:1-8.
13. Foxx RM, and Rubinoff, A. Behavioral treatment of caffeinism: reducing excessive coffee drinking. J App Behav.Anal. 1979;12:344-55.
14. James JE, Stirling K P, Hampton BAM. Caffeine fading: behavioral treatment of caffeine abuse. Behav Ther 1979;16:15-27.
15. James JE, Paull I, Cameron-Traub E, et al. Biochemical validation of self-reported caffeine consumption during caffeine fading. J Behav Med 1988;11:15-30.
16. Dana J, Loewenstein, G. A social science perspective on gifts to physicians from industry. JAMA 2003; 290:252–5.
Dr Castanyer1 wonders about the soundness of the advice she gives her patients about the reputed safety of moderate caffeine consumption during pregnancy. Her concerns regarding current clinical practice warrant consideration. I agree that “aging or prior medical history may act as confounders of negative pregnancy outcomes”. As reported in the review,2 numerous potential confounders have been examined (and often re-examined many times), including “diverse demographic variables, behaviour patterns, and living environment . . . age at conception, health status, pregnancy history, use of oral contraceptives, alcohol and other substance use, exposure to pollutants, maternal body mass, physical activity, religion, education, and occupation . . . pregnancy symptoms . . . potential recall bias and maternal cigarette smoking” (p. 5).2 However, as also reported in the review, caffeine-related negative pregnancy outcomes have repeatedly proven “robust to threats from potential confounding”.
In addition, Dr Castanyer suggests that any “change of medical recommendation” should await the outcome of randomised clinical trials. Again, that option is examined in the review, which includes a section headed, “Are Randomized Controlled Trials the Solution?” (pp. 5-6).2 However, as reported in the review, beyond the single trial conducted to date,3 it is doubtful whether mooted clinical trials will proceed due to ethical concerns over exposing pregnant women to caffeine, even at reput...
In addition, Dr Castanyer suggests that any “change of medical recommendation” should await the outcome of randomised clinical trials. Again, that option is examined in the review, which includes a section headed, “Are Randomized Controlled Trials the Solution?” (pp. 5-6).2 However, as reported in the review, beyond the single trial conducted to date,3 it is doubtful whether mooted clinical trials will proceed due to ethical concerns over exposing pregnant women to caffeine, even at reputedly “safe” levels.4 As the review explains, such concerns are ironic if not contradictory. Health authorities worldwide have promulgated the view that “moderate” caffeine consumption during pregnancy is safe. Were that view correct, there should be no ethical concerns. Nevertheless, though feasible, large-scale clinical trials to assess the consequences of maternal caffeine consumption appear unlikely. Accordingly, the principal evidence upon which we must rely is likely to continue to be that provided by observational studies, systematic review, meta-analysis, and (as with my review) narrative synthesis.
1. Castanyer MJG. Is this evidence enough to change our medical advice to coffee-consumer pregnant mothers? Evid Based Med 2020. Available: https://ebm.bmj.com/content/early/2020/09/01/bmjebm-2020-111432.responses.
2. James E. Maternal caffeine consumption and pregnancy outcomes: A narrative review with implications for advice to mothers and mothers-to-be. Evid Based Med 2020;25. Available: doi.org/10.1136/bmjebm-2020-111432.
3. Bech BH, Obel C, Henriksen TB, et al. Effect of reducing caffeine intake on birth weight and length of gestation: randomised controlled trial. BMJ 2007;334:409.
4. Jahanfar S, Jaafar SH. Effects of restricted caffeine intake by mother on fetal, neonatal and pregnancy outcomes. Cochrane Database Syst Rev 2015:CD006965.
Dr Fernando’s1 concerns about potential confounding from alcohol consumption and smoking do not warrant comment here as they are addressed in my review2 and summarised in my letter of reply to Murphy et al.3 A separate concern, shared by O’Connor4 and Murphy et al.,3 reveals Dr Fernando’s misguided presumption that narrative review is not “proper”. More specifically, while claiming that “a significant number of studies will have been missed” by my review, he cites no actual examples of publications he believes should have been included.
Additionally, along with O'Connor4 and Murphy et al.,3 Dr Fernando believes that prior publication renders authors biased when writing again on the same or similar topic. Pursuing the point, he injects an impugning embellishment regarding his claimed “insight into the motives of the author”. He refers to two books “about the dangers of caffeine”, a description that misrepresents the contents of those books and is a thinly veiled attempt at disparagement. The books are titled Caffeine and Health (1991)5 and Understanding Caffeine: A Biobehavioral Analysis (1997),6 respectively. Neither book is “about the dangers of caffeine”. On the contrary, both books seek to provide a comprehensive evidence-based biopsychosocial account of the most widely-consumed psychoactive substance in history, including reputed harms and benefits.
Dr Fernando finds it “interesting” that my review contains a description of just “one randomised contr...
Dr Fernando finds it “interesting” that my review contains a description of just “one randomised controlled trial”, ignoring the fact that to date only one such trial has been published. A previous review,7 which employed meta-analysis (Dr Fernando’s apparent favoured method), found the trial in question to be of limited value, and the reasons are reported in my review. Despite that, Dr Fernando asserts that my review somehow pre-emptively “discredited” that study. The claim is untrue, not least because the misattributed term, “discredited”, appears nowhere in my review. However, in the manner he himself suggests, the false claim raises questions about what his “motives” might be. Were Dr Fernando genuinely committed to meaningful discussion, direct engagement with the substance of the “message” (i.e., the scientific challenges of the topic before us) rather than irrelevant barbed comment aimed at the “messenger”, might have proved more constructive.
1. Fernando S. Bias in reporting. Evid Based Med 2020. Available: https://ebm.bmj.com/content/early/2020/09/01/bmjebm-2020-111432.responses.
2. James JE. Maternal caffeine consumption and pregnancy outcomes: A narrative review with implications for advice to mothers and mothers-to-be. Evid Based Med 2020;25. Available: doi.org/10.1136/bmjebm-2020-111432.
3. James JE. Caffeine and pregnancy: The need for calm reflection. Reply to Murphy et al. Evid Based Med 2020;25.
4. James JE. Caffeine and Pregnancy: Bias? Is the pot calling the kettle black? Reply to O'Connor. Evid Based Med 2020;25.
5. James JE. Caffeine and health. London: Academic Press, 1991.
6. James JE. Understanding caffeine: a biobehavioral analysis. Thousand Oaks, CA: Sage Publications, 1997.
7. Jahanfar S, Jaafar SH. Effects of restricted caffeine intake by mother on fetal, neonatal and pregnancy outcomes. Cochrane Database Syst Rev 2015:CD006965.
Dr O’Connor1 is concerned that I have published previous reviews, and in so doing may be biased. Indeed, I have published previous reviews, and my familiarity with the relevant literature has led me increasingly to question current relaxed attitudes towards caffeine consumption during pregnancy. The first review, published in 1985,2 reported that evidence available at that time tentatively supported the conclusion that caffeine may contribute to foetal growth restriction and low birth weight. That review highlighted methodological shortcomings in the then extant literature, and called for more research employing improved methods for measuring caffeine exposure and better controls against potential confounders.
An updated review, in 1991,3 found that more and improved research had been published since the earlier review, and that the overall evidence of caffeine-related negative pregnancy outcomes had strengthened. With a subsequent update in 1997,4 it was concluded that the evidence against maternal caffeine consumption had become strong. The latest review5 reported that the balance of evidence, including findings from original observational studies and meta-analyses, supported the conclusion that consumption of caffeine during pregnancy increases the risk of several serious negative pregnancy outcomes. Perversely, Dr O’Connor appears to believe that familiarity with research implies bias. In fact, my conclusions evolved over time, and the direction of that evolutio...
An updated review, in 1991,3 found that more and improved research had been published since the earlier review, and that the overall evidence of caffeine-related negative pregnancy outcomes had strengthened. With a subsequent update in 1997,4 it was concluded that the evidence against maternal caffeine consumption had become strong. The latest review5 reported that the balance of evidence, including findings from original observational studies and meta-analyses, supported the conclusion that consumption of caffeine during pregnancy increases the risk of several serious negative pregnancy outcomes. Perversely, Dr O’Connor appears to believe that familiarity with research implies bias. In fact, my conclusions evolved over time, and the direction of that evolution was dictated by accumulating evidence of harm. Thus, the overall trajectory of my conclusions reflects the normal progression of scientific knowledge.
While claiming that the review lacks features characteristic of systematic review and meta-analysis, claims repeated by Fernando6 and Murphy et al.,7 O’Connor fails (as do those other authors) to acknowledge the continuing legitimacy of the “traditional” or narrative review. In particular, he fails to acknowledge that the literature examined in my review is substantially comprised of prior systematic reviews and meta-analyses. It is important to choose a review format that reflects the current state of knowledge. As such, my latest review is a response to current need for previous literature to be synthesised conceptually, which I judged could be best achieved by way of narrative review. Unfortunately, Dr O’Connor appears not to appreciate that in common with review practice in general, narrative review seeks to provide a comprehensive, critical, and objective analysis of current knowledge. It is wrong to assume that systematic review (so-called) and meta-analysis are necessarily superior to narrative review at all times and under all circumstances.
1. O’Connor RF. Insufficiently robust methodology and risk of bias. Evid Based Med 2020. Available: https://ebm.bmj.com/content/early/2020/09/01/bmjebm-2020-111432.responses.
2. James JE, Paull I. Caffeine and human reproduction. Rev Environ Health 1985;5:151–67.
3. James JE. Caffeine and health. London: Academic Press, 1991.
4. James JE. Understanding caffeine: a biobehavioral analysis. Thousand Oaks, CA: Sage Publications, 1997.
5. James E. Maternal caffeine consumption and pregnancy outcomes: A narrative review with implications for advice to mothers and mothers-to-be. Evid Based Med 2020;25. Available: doi.org/10.1136/bmjebm-2020-111432.
6. James JE. Caffeine and pregnancy: Don’t shoot the messenger, please. Reply to Fernando. Evid Based Med 2020;25.
7. James JE. Caffeine and pregnancy: The need for calm reflection. Reply to Murphy et al. Evid Based Med 2020;25.
In his narrative review of the association between maternal caffeine consumption and pregnancy outcomes, Professor Jack E James claimed there was sufficient evidence of harmful causal effects to suggest that pregnant women or women contemplating pregnancy should 'avoid caffeine' (1). His opinions were widely reported by the media in line with a sensational press release that claimed there was "No safe level of caffeine consumption for pregnant women and would-be mothers". We do not however consider these claims to be appropriate or justified, due to a number of serious methodological limitations, statistical errors, and a concerning lack of objectivity. The author declared no conflicts of interest, yet has written extensively on the 'lethality' of caffeine (2). For this, and the following reasons, we believe the review and its recommendations should be interpreted with extreme caution.
1. Scientific conduct
a) The article is described as a ‘narrative review’, and thus by its nature, falls well short of the standards expected for a formal systematic scientific review of the literature. It is not clear how the author identified articles for inclusion, nor what criteria were used for exclusion, or what approach, if any, was used to critically appraise the studies identified or synthesise the information obtained. It is therefore difficult to have confidence that the articles presented offer an unbiased reflection of the literature an...
1. Scientific conduct
a) The article is described as a ‘narrative review’, and thus by its nature, falls well short of the standards expected for a formal systematic scientific review of the literature. It is not clear how the author identified articles for inclusion, nor what criteria were used for exclusion, or what approach, if any, was used to critically appraise the studies identified or synthesise the information obtained. It is therefore difficult to have confidence that the articles presented offer an unbiased reflection of the literature and that equal scepticism was applied to the evaluation of each article identified. If the article was intended as a ‘review of reviews’ - which would have been merited by the number of systematic reviews and meta-analyses discovered - then we would have expected much more critical engagement with the limitations of each review and how these are addressed, if at all, by the different approaches used.
b) The author does not appear to demonstrate the level of self-scepticism required for an investigation of this nature. More space, for example, is devoted to discussing the potential mechanism through which caffeine may cause harm rather than considering the various ways in which such an association may be observed through non-direct means. The inductive scientific method dictates a sceptical approach to the generation of theory, with confidence gained from a theory’s resilience to alternative hypotheses. In order to provide evidence that caffeine causes adverse pregnancy outcomes, the article should therefore have focussed primarily on discounting all other possible explanations. Instead, the review primarily focuses on uncritically reporting those findings that appear to support the primary hypothesis; sometimes placing James in conflict with the original interpretation of the study being cited. For example, Gaskins et al’s 2018 is cited as showing an association between maternal caffeine consumption and miscarriage, yet Gaskins et al state that a “component other than caffeine could be driving the association” (3). Similarly, Greenwood et al 2014 (4) describe any potential effects observed as being ‘minimal’ or ‘modest’, yet this is dismissed without quantification by simply stating that ‘In reality...the cumulative population impact... are demonstrably neither 'modest' nor 'minimal'.
c) From previous reviews, such as Greenwood et al 2014, it seems clear that caffeine intake is associated with a higher risk of adverse pregnancy outcome. However, whether this reflects a causal effect is unresolved. In his discussion, James claims “likely causation is supported by a compelling body of evidence”, and speculates that industry may be involved in feeding doubts of this conclusion. Unfortunately, this claim grossly underestimates the challenge of making causal inference from observational data. James highlights ‘potential confounding or misclassification’ as threats to causal inference and identifies smoking as a prominent potential confounder. Since most studies make some effort to control for smoking, James states that “concerns about smoking as a source of confounding have been conclusively disconfirmed”. This however disregards the possibility of residual confounding, either due to a lack of accurate and detailed information, flawed adjustment strategies, or both. Studies that have used Mendelian Randomisation or negative control designs strongly suggest that smoking causes both caffeine consumption (5) and fetal outcomes (6-7). However, it has also been demonstrated that self-reported smoking does not adequately control for confounding (8-9). It therefore seems very likely that every study that either failed to adjust for maternal smoking, or used self-reported information - and every meta-analysis that included such studies - will be biased by residual confounding. Other confounders besides smoking are of course also likely to contribute to the observed association, and will similarly suffer from a risk of residual confounding if not properly measured or adjusted. In general, studies that have not used robust causal inference approaches, such as causal diagrams or Mendelian Randomisation, should not be considered to provide evidence of causal effects. This is not changed by the existence of a ‘dose response’ relationship, which by itself offers negligible proof that a relationship is directly causal (10).
d) Although establishing a causal effect of caffeine on one or more adverse pregnancy outcomes would be scientifically valuable, the public health implications - and justification for any policy recommendations - would still depend on the size of any such effect. In this regard, James’ review again falls short of providing any insight beyond what can be found elsewhere. Greenwood et al 2014, for example, are clear that any true effect is likely to be minimal or modest, and therefore suggest that while upper limits of intake may be justified there is no reason to modify the existing message of moderation. No similar real-world nuance is present in James’ review, which also did not report or attempt to estimate absolute risks, which are far easier to interpret than risk ratios, particularly for rare outcomes such as childhood acute leukaemia (11).
2. The findings and recommendations do not account for the lived realities of women’s lives
a) Evidence from the WRISK Project (12) (forthcoming) shows that alarmist media headlines on pregnancy-related public health advice cause immense anxiety and guilt for pregnant women and mothers, particularly those who have experienced a pregnancy loss or poor outcome. The author’s claim that 280,000 of the approximately 1 million miscarriages that take place in the USA each year are attributable to maternal caffeine consumption is a shocking extrapolation which will undoubtedly cause many women extreme anxiety, and may lead them to blame themselves for what is likely to be an unavoidable pregnancy loss (13). This inaccurate extrapolation is extremely irresponsible and in direct contradiction of the principle to ‘do no harm’ in health research.
b) Policy recommendations and public health advice that arise from research must be thoughtfully considered and account for the complex circumstances in which people live their lives. It is not practical or desirable for all people planning a pregnancy, or who are pregnant, to completely avoid caffeine consumption. Many women value and use a precautionary approach when it comes to their pregnancies, but there is a growing body of evidence to suggest that public health advice to abstain completely from a wide range of substances leads to fatigue and anxiety. Some women may be less likely to follow advice as a result (14).
3. The press release accompanying the paper was sensationalist
a) The press release led with “No safe level of caffeine consumption for pregnant women and would-be mothers”, which is an overstatement of the findings.
b) The press release was not clear about the methods of the paper, which is essentially expert opinion rather than a systematic review of the existing research.
c) You will be aware of the media headlines that often result from new studies, particularly those relating to pregnancy. Existing and forthcoming evidence (15-16) suggests that journalists use information taken directly from journal or university press releases to write their articles and bylines, rather than sensationalising study results themselves. In order to prevent irresponsible or inaccurate reporting, press releases must be transparent about research methods, clearly state where evidence is weak, and contextualise the risk that is reported in the paper (e.g. by providing a comment on absolute risk). The pursuit for impact and media coverage must not trump our responsibility to provide evidence-based, transparent information to the public. Indeed, evidence suggests that aligning press releases with the evidence, being cautious about claims, and including caveats does not harm “news interest” (17).
1. James J E.Maternal caffeine consumption and pregnancy outcomes: a narrative review with implications for advice to mothers and mothers-to-be. BMJ Evidence-Based Medicine Published Online First: 25 August 2020. doi: 10.1136/bmjebm-2020-111432
2. James J E. Death By Caffeine: How Many Caffeine-Related Fatalities and Near-Misses Must There Be Before We Regulate? Journal of Caffeine Research. Dec 2012.149-152.http://doi.org/10.1089/jcr.2013.1226
3. Gaskins AJ, Rich-Edwards JW, Williams PL, Toth TL, Missmer SA, Chavarro JE. Pre-pregnancy caffeine and caffeinated beverage intake and risk of spontaneous abortion. Eur J Nutr. 2018;57(1):107-117. doi:10.1007/s00394-016-1301-2
4. Greenwood DC, Thatcher NJ, Ye J, et al. Caffeine intake during pregnancy and adverse birth outcomes: a systematic review and dose-response meta-analysis. Eur J Epidemiol. 2014;29(10):725-734. doi:10.1007/s10654-014-9944-x
5. Shipton, D. et al. Reliability of self-reported smoking status by pregnant women for estimating smoking prevalence: a retrospective, cross sectional study. BMJ 339, (2009).
6. Bjørngaard, J. H. et al. Heavier smoking increases coffee consumption: findings from a Mendelian randomization analysis. International Journal of Epidemiology 46, 1958–1967 (2017).
7. Tyrrell, J. et al. Genetic variation in the 15q25 nicotinic acetylcholine receptor gene cluster (CHRNA5–CHRNA3–CHRNB4) interacts with maternal self-reported smoking status during pregnancy to influence birth weight. Hum Mol Genet 21, 5344–5358 (2012).
8. England, L. et al. Misclassification of maternal smoking status and its effects on an epidemiologic study of pregnancy outcomes. Nicotine & Tobacco Res. 9, 1005–1013 (2007).
9. Munafò, M. R. et al. Association Between Genetic Variants on Chromosome 15q25 Locus and Objective Measures of Tobacco Exposure. J Natl Cancer Inst 104, 740–748 (2012).
10. Rothman KJ, Greenland S. Hill’s Criteria for Causality. Encyclopedia of Biostatistics. [Online] John Wiley & Sons, Ltd; 2005. Available from: doi:10.1002/0470011815.b2a03072
11. How to communicate benefits, risks and uncertainties. Patient Information Forum. Revised August 2019 www.pifonline.org.uk
13. Pollock D, Ziaian T, Pearson E, Cooper M, Warland J. Understanding stillbirth stigma: A scoping literature review. Women and Birth. 2020;33(3):207-218.
14. Grant A, Morgan M, Gallagher D, Mannay D. Smoking during pregnancy, stigma and secrets: Visual methods exploration in the UK. Women and Birth. 2020;33(1):70-76. doi.org/10.1016/j.wombi.2018.11.012
15. Bratton L, Adams RC, Challenger A et al. The association between exaggeration in health-related science news and academic press releases: a replication study [version 2; peer review: 2 approved]. Wellcome Open Res 2019, 4:148 (https://doi.org/10.12688/wellcomeopenres.15486.2)
16. Sumner P, Vivian-Griffiths S, Boivin J, et al. Exaggerations and Caveats in Press Releases and Health-Related Science News. PLoS One. 2016;11(12):e0168217. Published 2016 Dec 15. doi:10.1371/journal.pone.0168217
17. Adams RC, Challenger A, Bratton L, et al. Claims of causality in health news: a randomised trial. BMC Med. 2019;17(1):91. Published 2019 May 16. doi:10.1186/s12916-019-1324-7