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...
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 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).
ENDS.
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
Usman et al (1) write that only one of the 18 studies of COVID-19 patients they included in their review of the Smoker's Paradox reported that "the prevalence of smokers resembles that of the general population."
But this study--by Richardson et al in New York City (2)--actually only reported the prevalence of "never smokers" at 84.4%. It did not distinguish between current and former smokers among the remaining 15.6%, however, so Usman et al should have marked this combined result with an asterisk in their Table 1. Far from resembling the general population, the 15.6% combined rate is less than half the 34% expected in USA, where approximately 14% are current and 20% former smokers. With this correction, all 18 studies support the Smoker’s Paradox, which belies the authors’ conclusion that a “protective effect should NOT be inferred” [emphasis added].
The protective effect is clearly real and further supported by the largest study of COVID-19 to date (n=7,162) with data on smoking status (3), which Usman et al did not include in their review. Current smokers in this CDC study comprised just 1.3% of all the COVID-19 patients seeking care from US hospitals in 50 states and Washington DC, 1.2% of those treated as outpatients, and 1.1% of those treated in intensive care units.
Usman et al also did not mention the compound most likely responsible for the protective effects of smoking against respiratory infections, which...
Usman et al (1) write that only one of the 18 studies of COVID-19 patients they included in their review of the Smoker's Paradox reported that "the prevalence of smokers resembles that of the general population."
But this study--by Richardson et al in New York City (2)--actually only reported the prevalence of "never smokers" at 84.4%. It did not distinguish between current and former smokers among the remaining 15.6%, however, so Usman et al should have marked this combined result with an asterisk in their Table 1. Far from resembling the general population, the 15.6% combined rate is less than half the 34% expected in USA, where approximately 14% are current and 20% former smokers. With this correction, all 18 studies support the Smoker’s Paradox, which belies the authors’ conclusion that a “protective effect should NOT be inferred” [emphasis added].
The protective effect is clearly real and further supported by the largest study of COVID-19 to date (n=7,162) with data on smoking status (3), which Usman et al did not include in their review. Current smokers in this CDC study comprised just 1.3% of all the COVID-19 patients seeking care from US hospitals in 50 states and Washington DC, 1.2% of those treated as outpatients, and 1.1% of those treated in intensive care units.
Usman et al also did not mention the compound most likely responsible for the protective effects of smoking against respiratory infections, which is not nicotine but carbon monoxide (CO). Several studies of using gaseous CO or CO releasing molecules as drugs to treat respiratory diseases have been published recently and more are registered at ClinicalTrials.gov.
Non-smokers seeking to ward off infection by SARS-COv2 need not start smoking, however. They can boost their endogenous production of CO simply by ingesting hemin, vitamin C, curcumin, or other supplements known to increase the expression and activity of heme oxygenase-1.(4) This releases equimolar amounts of CO, biliverdin that is converted to bilirubin, iron that is convert to ferritin, and three times as much water.
Too much CO exposure from any source causes tissue hypoxia, however, as CO binds more than aggressively than oxygen to cytochrome oxidase. This can be fatal if not detected and reversed before vital organs shut down. The risk of death correlates less with arterial or venous CO alone, however, than the difference between them, so I urge COVID-19 clinicians to start measuring both.(5)
References
1) Usman MS, Siddiqi TJ, Khan MS, et al. Is there a smoker’s paradox in COVID-19? BMJ Evidence-Based Medicine Published Online First: 11 August 2020. doi: 10.1136/bmjebm-2020-111492
2) Richardson S, Hirsch JS, Narasimhan M, et al. Presenting characteristics, comorbidities, and outcomes among 5700 patients hospitalized with COVID-19 in the New York City area. JAMA 2020;323:2052–9
3) Chow N, Fleming-Dutra K, Gierke R, et al. [aka CDC COVID-19 Response Team] Preliminary Estimates of the Prevalence of Selected Underlying Health Conditions Among Patients with Coronavirus Disease 2019 — United States, February 12–March 28, 2020. MMWR Morb Mortal Wkly Rep 2020;69:382–386. DOI: http://dx.doi.org/10.15585/mmwr.mm6913e2
4) Barbagallo I, Galvano F, Frigiola A, et al. Potential therapeutic effects of natural heme oxygenase-1 inducers in cardiovascular diseases. Antioxid Redox Signaling 2013 Feb 10;18(5):507-21. doi: 10.1089/ars.2011.4360.
5) Donnay A. Toxicologist warns COVID-19 patients are dying of carbon monoxide poisoning that pulse oximeters cannot distinguish and both oxygen therapy and ventilators are making worse. Medium 2020; April 9. Available: https://medium.com/@albertdonnay_17627/toxicologist-warns-covid-19-patients-are-dying-of-carbon-monoxide-poisoning-that-pulse-oximeters-a2ac42d4c3a4 [Accessed 2 September 2020]
Dear Editor,
Recent literature suggested increased risk of severe COVID-19 in smokers which also got affirmation from World Health Organization (WHO) [1, 2]. However, original peer reviewed research which explained pathophysiological basis of the enhanced COVID-19 severity in smokers is currently scarce. Increased expression of SARS-CoV-2 cell entry receptor ACE2 in respiratory tract and lung tissue of smokers unraveled from analysis of gene expression data was used to predict higher chances of SARS-CoV-2 infection but that failed to explain enhanced COVID-19 severity [3]. Few authors have suggested that increased risk of severe complications and higher mortality rate in infected smokers may be due to host-specific factors like weakening of respiratory health and immunity caused by chronic smoking [4]. However, none of the virus-related factors which can be responsible for the COVID-19 severity in smokers has been reported until date. Based on the recent research updates on SARS-CoV-2 specific virulence in host cells, we propose a plausible mechanism which associates smoking with increased severity of COVID-19.
Apart from a cell surface entry receptor, coronaviruses require furin (a host protease) mediated cleavage of their spike (S) protein for successful invasion of the host cell. SARS-CoV-2, a member of the genus betacoronaviruses, has evolved a unique furin protease S1/S2 cleavage site, which is absent in other family members, including SARS-CoV-1 [5]. Rec...
Dear Editor,
Recent literature suggested increased risk of severe COVID-19 in smokers which also got affirmation from World Health Organization (WHO) [1, 2]. However, original peer reviewed research which explained pathophysiological basis of the enhanced COVID-19 severity in smokers is currently scarce. Increased expression of SARS-CoV-2 cell entry receptor ACE2 in respiratory tract and lung tissue of smokers unraveled from analysis of gene expression data was used to predict higher chances of SARS-CoV-2 infection but that failed to explain enhanced COVID-19 severity [3]. Few authors have suggested that increased risk of severe complications and higher mortality rate in infected smokers may be due to host-specific factors like weakening of respiratory health and immunity caused by chronic smoking [4]. However, none of the virus-related factors which can be responsible for the COVID-19 severity in smokers has been reported until date. Based on the recent research updates on SARS-CoV-2 specific virulence in host cells, we propose a plausible mechanism which associates smoking with increased severity of COVID-19.
Apart from a cell surface entry receptor, coronaviruses require furin (a host protease) mediated cleavage of their spike (S) protein for successful invasion of the host cell. SARS-CoV-2, a member of the genus betacoronaviruses, has evolved a unique furin protease S1/S2 cleavage site, which is absent in other family members, including SARS-CoV-1 [5]. Recently, Anand et al in a bioinformatics based analysis, showed that S1/S2 cleavage site of SARS-CoV-2 has striking similarity to the Furin-cleavable peptide on the human epithelial sodium channel α-subunit (ENaC-α). ENaC is present in the lung pneumocytes, where they have a physiological role in fluid clearance from the alveoli. ENaC has established roles in immune cell activation, and cytokine/chemokine mediated ARDS in inflammatory disorders [6, 7]. Furin is also required for proteolytic activation of ENaC by cleavage of extracellular domain of its α subunit [8]. SARS-CoV-2 in the infecting the pneumocytes can compete for Furin thus can inhibit proteolytic activation of ENaC, which will result in fluid accumulation inside the alveoli leading to pulmonary edema and acute respiratory distress syndrome (ARDS). Existing literature suggests that cigarette smoke condensate [9], more specifically its major ingredient Crotonaldehyde (CRO), can cause does-dependent inhibition of ENaC-α subunit expression in pneumocytes leading to edematous acute lung injury [10]. Reduced availability of active ENaC in smokers may get further exacerbated if they get infected with SARS-CoV-2 owing to virus mediated inactivation of this ion channel, making them vulnerable for developing severe COVID-19 symptoms (Fig. 1b). To note, the current smokers may be at increased risk of developing severe COVID-19 symptoms owing to the abundance of freshly released smoke condensates in their lungs leading to greater inhibition of ENaC in pneumocytes. Recent literature does suggest a higher risk of severe complications and a higher mortality rate among current smokers hospitalized with COVID-19 [2]. Our proposed mechanism is an effort to explain SARS-CoV-2 based etiology of increased disease severity in smokers, which was not discussed before and can have important implications for therapeutic management and health policy decisions for COVID-19.
Conflict of Interst
Authors declared no conflict of interest
References:
1. Smoking and COVID-19 [Internet]. [cited 2020 Jun 11].Available from: https://www.who.int/news-room/commentaries/detail/smoking-and-covid-19.
2. Alqahtani JS, Oyelade T, Aldhahir AM, Alghamdi SM, Almehmadi M, Alqahtani AS, Quaderi S, Mandal S, Hurst JR. Prevalence, Severity and Mortality associated with COPD and Smoking in patients with COVID-19: A Rapid Systematic Review and Meta-Analysis. Bhatt GC, editor. PLoS One; 2020; 15: e0233147Available from: https://dx.plos.org/10.1371/journal.pone.0233147.
3. Muus C, Luecken MD, Eraslan G, Waghray A, Heimberg G, Sikkema L, Kobayashi Y, Vaishnav ED, Subramanian A, Smilie C, Jagadeesh K, Duong ET, Fiskin E, Triglia ET, Ansari M, Cai P, Lin B, Buchanan J, Chen S, Shu J, Haber AL, Chung H, Montoro DT, Adams T, Aliee H, Samuel J, Andrusivova AZ, Angelidis I, Ashenberg O, Bassler K, et al. Integrated analyses of single-cell atlases reveal age, gender, and smoking status associations with cell type-specific expression of mediators of SARS-CoV-2 viral entry and highlights inflammatory programs in putative target cells. bioRxiv Cold Spring Harbor Laboratory; 2020; : 2020.04.19.049254.
4. van Zyl-Smit RN, Richards G, Leone FT. Tobacco smoking and COVID-19 infection. Lancet. Respir. Med. Elsevier; 2020;S2213-2600(20)30239-3. doi:10.1016/S2213-2600(20)30239-3.
5. Coutard B, Valle C, de Lamballerie X, Canard B, Seidah NG, Decroly E. The spike glycoprotein of the new coronavirus 2019-nCoV contains a Furin-like cleavage site absent in CoV of the same clade. Antiviral Res. Elsevier B.V.; 2020; 176: 104742.
6. Wynne BM, Zou L, Linck V, Hoover RS, Ma HP, Eaton DC. Regulation of lung epithelial sodium channels by cytokines and chemokines. Front. Immunol. Frontiers Media S.A.; 2017; 8.
7. Mutchler SM, Kleyman TR. New insights regarding epithelial Na+ channel regulation and its role in the kidney, immune system and vasculature. Curr. Opin. Nephrol. Hypertens. Lippincott Williams and Wilkins; 2019. p. 113–119.
8. Anand P, Puranik A, Aravamudan M, Venkatakrishnan AJ, Soundararajan V. SARS-CoV-2 strategically mimics proteolytic activation of human ENaC. Elife [Internet] 2020; 9:e58603. doi:10.7554/eLife.58603.
9. Xu H, Ferro TJ, Chu S. Cigarette smoke condensate inhibits ENaC α-subunit expression in lung epithelial cells. Eur. Respir. J. European Respiratory Society; 2007; 30: 633–642.
10. Li Y, Chang J, Cui Y, Zhao R, Ding Y, Hou Y, Zhou Z, Ji HL, Nie H. Novel mechanisms for crotonaldehyde-induced lung edema. Oncotarget Impact Journals LLC; 2017; 8: 83509–83522.
Figure Legends:
Figure 1 a. Normal pneumocytes maintain alveolar fluid resorption with the help of Furin proteolysis activated ENaC, b. Cigarette smoke condensate directly inhibits ENaC while SARS-CoV-2 competes for its Furin mediated proteolysis thus prevents its activation.
First available online on August 18, 2020 in BMJ Evidence-Based Medicine, Aronson and Ferner (1) concluded that women using hormonal contraceptives cannot rely on their contraceptive method if they take a short course of non-enzyme inducing antibiotics based on Yellow Card reports to the UK’s Medicines and Healthcare products Regulatory Agency.
We believe that there are fundamental scientific issues and limitations with this study not adequately addressed by the authors. First, Yellow Card reports require provider reporting of an unintended pregnancy, which the authors acknowledge are subject to reporting bias. As the authors also acknowledge, many healthcare providers suspect there are drug-drug interactions between hormonal contraception and all antibiotics, despite the lack of definitive evidence (1). Therefore, there already exists a bias among providers that they would suspect and report an unintended pregnancy attributed to a drug-drug interaction among women taking antibiotics. The medications in each group are also not equivalent and bias the sample. For example, in the antibiotic group, metronidazole and nitrofurantoin are more commonly used in younger reproductive-aged and sexually active women (2,3), the population at highest risk of unintended pregnancies (4). In comparison, the control group includes such medications as propranolol and theophylline, which are used for treatment of cardiac and respiratory conditions more common among older women (5,6), wi...
First available online on August 18, 2020 in BMJ Evidence-Based Medicine, Aronson and Ferner (1) concluded that women using hormonal contraceptives cannot rely on their contraceptive method if they take a short course of non-enzyme inducing antibiotics based on Yellow Card reports to the UK’s Medicines and Healthcare products Regulatory Agency.
We believe that there are fundamental scientific issues and limitations with this study not adequately addressed by the authors. First, Yellow Card reports require provider reporting of an unintended pregnancy, which the authors acknowledge are subject to reporting bias. As the authors also acknowledge, many healthcare providers suspect there are drug-drug interactions between hormonal contraception and all antibiotics, despite the lack of definitive evidence (1). Therefore, there already exists a bias among providers that they would suspect and report an unintended pregnancy attributed to a drug-drug interaction among women taking antibiotics. The medications in each group are also not equivalent and bias the sample. For example, in the antibiotic group, metronidazole and nitrofurantoin are more commonly used in younger reproductive-aged and sexually active women (2,3), the population at highest risk of unintended pregnancies (4). In comparison, the control group includes such medications as propranolol and theophylline, which are used for treatment of cardiac and respiratory conditions more common among older women (5,6), with known decreased fertility (7). Without any summary demographic information about these populations (e.g. age, socioeconomic status), we cannot assume that the control and exposure groups have equivalent baseline risk for unintended pregnancies.
The rates of unintended pregnancy reported in each of the groups (0.009% in controls, 0.062% in the antibiotic group, 0.12% in the enzyme-inducing group) (1) are also much lower than expected in general users of oral contraception. The failure rate with typical use of oral contraceptives is approximately 7% and 0.3% with perfect use (8). While the authors note that absolute risks cannot be calculated from this data, caution needs to be taken interpreting data that is vastly disparate from known actual use data. Lastly, the article proposes mechanisms to explain the potential interaction between oral contraceptives and antibiotics focusing on how drug interactions affect estrogen levels in oral contraceptives. Pharmacologically, the progestin component of combined oral contraceptives provides the main contraceptive effect (8). Furthermore, progestins do not rely on enterohepatic recirculation like estrogens, and thus antibiotic-induced gastrointestinal changes would not affect the efficacy of these progestins (9,10).
Without scientifically rigorous data, it is important to not create false concern for women taking oral contraceptives and prescribed non-enzyme inducing antibiotics. While we agree that further research is needed in this area, there are significant limitations to this study that greatly reduce its applicability to actual clinical practice.
References:
1.) Aronson JK, Ferner RE. Analysis of reports of unintended pregnancies associated with the combined use of non-enzyme-inducing antibiotics and hormonal contraceptives. BMJ Evidence-Based Medicine Published Online First: 18 August 2020. Doi: 10.1136/bmjebm-2020-111363.
2.) Tinker SC, Broussard CS, Frey MT, Gilboa SM. Prevalence of Prescription Medication Use among Non-Pregnant Women of Childbearing Age and Pregnancy Women in the United States – NHANES, 1999-2006. Maternal and Child Health Journal 2015; 19(5): 1097-1106.
3.) Palmsten K, Hernandez-Diaz S, Chambers CD, Mogun H, Lai S, Gilmer TP, Huybrechts KF. The Most Commonly Dispensed Prescription Medications Among Pregnant Women Enrolled in the United States Medicaid Program. Obstetrics and Gynecology 2015; 126(3): 465-473.
4.) Unintended Pregnancy in the United States. Guttmacher Institute, 2019. https://www.guttmacher.org/fact-sheet/unintended-pregnancy-united-states. Accessed August 28, 2020.
5.) Martin CB, Hales CM, Qiuping G, Ogden CL. Prescription drug use in the United States, 2015-2016. NCHS Data Brief 2019; 334: 1-8.
6.) Henriksen DP, Davidsen JR, Laursen CB. Nationwide use of theophylline among adults – A 20-year Danish drug utilization study. Respiratory Medicine 2018; 140: 57-62.
7.) American College of Obstetricians and Gynecologic Practice and Practice Committee. Female age-related fertility decline. Committee Opinion No. 589. Fertility and Sterility 2014; 101(3): 633-634.
8.) Cwiak C, Edelman A. Combined Oral Contraceptives (COCs). In: Contraceptive Technology, 21st ed, Hatcher RA, Nelson AL, Trussell J, et al. Ayer Company Publishers, Inc., New York 2018.
9.) Orme ML, Back DJ. Factors affecting the enterohepatic circulation of oral contraceptive steroids. American Journal of Obstetrics and Gynecology 1990; 163(6): 2146-52.
10.) Elomaa K, Ranta S, Tuominen J, Lahteenmaki P. The possible role of enterohepatic cycling on bioavailability of norethisterone and gestodene in women using combined oral contraceptives. Contraception 2001; 63(1): 13-18.
In my daily practice that is limited, I've been allowing my patients to drink two cups of coffee a day, although they tend to be restrictive when applying my advice. Most of them are healthy women in their 30s. Whenever they've had a bad result, it has been attributed to other causes. When reading your impeccable research work, I've missed some comment on the clinical relevance of certain outcomes as a minor change in birth weight; moreover, aging or prior medical history may act as confounders of negative pregnancy outcomes. I appreciate your effort very much, but I consider the change of medical recommendations requires a more in-depth assessment, by means of one or more randomized clinical trials. Let's bear in mind than in my home country, Spain, temperatures in summer may be unbearable if you are an active working mother-to-be. And, definitely, our medical role is to give evidence-based solutions and avoid changing our pieces of advice every couple of years.
‘There is no safe level of caffeine intake in pregnancy’. That is the conclusion of this ‘narrative review’ of caffeine safety in pregnancy (BMJ Evidence Based Medicine, Open Access) which a patient brought to my attention very recently after hearing about it on the mainstream media. I felt that it requires clarification to avoid concern amongst the general public and those unable to analyse and critically appraise the literature.
The single author concluded that, after finding 48 studies (37 observational studies and 11 meta-analyses), caffeine intake in pregnancy significantly increases the risk of miscarriage, stillbirth, low birth weight, childhood leukaemia and childhood overweight/obesity. The author then goes on to recommend that all worldwide guidelines (including American, UK and Australian) stating the safety of caffeine in doses<200mg/day (approximately 2 cups of coffee) should be revised to say ‘there is no safe level of caffeine in pregnancy’.
However, there is no need to panic, which appears to be the response of the mainstream media and patients from the general population. Very soon after publication, this paper was picked up by several news outlets including CNN, The Guardian and also on a number of social media streams. Women were being told not to drink coffee in pregnancy the same way they were being told not to drink alochol.
This paper is far from as conclusive as it tries to make the reader believe, but serves as a good exampl...
‘There is no safe level of caffeine intake in pregnancy’. That is the conclusion of this ‘narrative review’ of caffeine safety in pregnancy (BMJ Evidence Based Medicine, Open Access) which a patient brought to my attention very recently after hearing about it on the mainstream media. I felt that it requires clarification to avoid concern amongst the general public and those unable to analyse and critically appraise the literature.
The single author concluded that, after finding 48 studies (37 observational studies and 11 meta-analyses), caffeine intake in pregnancy significantly increases the risk of miscarriage, stillbirth, low birth weight, childhood leukaemia and childhood overweight/obesity. The author then goes on to recommend that all worldwide guidelines (including American, UK and Australian) stating the safety of caffeine in doses<200mg/day (approximately 2 cups of coffee) should be revised to say ‘there is no safe level of caffeine in pregnancy’.
However, there is no need to panic, which appears to be the response of the mainstream media and patients from the general population. Very soon after publication, this paper was picked up by several news outlets including CNN, The Guardian and also on a number of social media streams. Women were being told not to drink coffee in pregnancy the same way they were being told not to drink alochol.
This paper is far from as conclusive as it tries to make the reader believe, but serves as a good example of how language can be used to persuade when evidence does not.
This ‘study’ is not a properly conducted systematic review or metanalysis and to publish it as an ''evidence synthesis'' is dangerous, as it implies a level of rigor which is not demonstrated. Literature from only PubMed and Google Scholar were searched. The search was not systematically or transparently documented and there was no reference to the PRISMA guidelines. This is important as it means that a significant number of studies will have been missed in the search, introducing significant reporting bias (studies with results showing caffeine is safe in pregnancy may not have been included).
The paper looks at both observational studies and meta-analyses and it is not clear whether non-independence has been accounted for – that is, some of the individual studies may have been included in the reported metanalyses. This would result in duplication of the data and an overestimation of the effect size. Because the review was not systematic, there is no detailed analysis of confounding factors (ie. Women who drank alcohol or smoked as well as drank coffee during their pregnancy which could also effect the outcomes). The variation between the studies have not been reported or investigated (therefore, cannot be compared or summed). This ‘heterogeneity’ has not been identified or reported. There is no consideration of publication bias (when only studies with positive results tend to get published), and even more importantly, no analysis of bias in each individual study (which is mandatory for any meta-analysis).
The author appears to try to make conclusions based on the ‘number of studies that found an effect’ instead of the ‘number of participants that were effected’. It also doesn't account for the quality or lack of quality of each study. Even if a lot of studies find an effect, if they are not well designed then the effect may not exist.
This paper seems to be written without any balance, making one concerned about the agenda of the author. The author states that the safety of caffeine may be supported by caffeine corporations (coffee and soft drink manufacturers). Indeed, a quick ‘Google’ search of the author’s name shows that he has written two books about the dangers of caffeine. While this does not mean that this report can be discounted, it does give some insight into the motives of the author.
Interestingly, one randomised controlled trial which found no effect of caffeine in pregnancy is briefly mentioned in the discussion of the study, but quickly ‘discredited’.
In short, this ''narrative review'' has probably gained far more media attention than was initially intended, however, the overarching and far-reaching consequences of this are significant when the evidence behind its recommendations is non-systematic and biased. Publication of such work should be discouraged, as the impact on the general population cannot be underestimated.
Editor,
I welcome this publication with it's focus on a potentially important cause of adverse pregnancy outcomes.
This study has several methodological faults that need to be declared and addressed.
The study's single author has written extensively on this topic over the last 29 years. He cites several of his own publications in the paper, As far as I can judge, they are all critical of caffeine in pregnancy. Surely this puts him at risk of bias.
The best way to address such bias is to conduct a systematic review with precise methodology. Also, at least one other author should be involved in assessing suitability of the papers, and minimising bias.
Only English language papers are studied.
Only PubMed and Google Scholar are searched. No reference is made to other important databases such as CDSR, Medline, EMBASE and CINAHL.. There does not appear to have been any pre-specified eligibility criteria in assessing whether or not studies should be included in the review e.g. community based populations or pre defined study methods.
There is no attempt made to assess the quality of the studies used in writing the paper.
The search strategy appears vague.
The results in table 1 give odds ratio but there is no quantification of this. What we need is absolute risk with numbers needed to harm. If this figure cannot be calculated then we should be told and given the reasons why.
Editor,
I welcome this publication with it's focus on a potentially important cause of adverse pregnancy outcomes.
This study has several methodological faults that need to be declared and addressed.
The study's single author has written extensively on this topic over the last 29 years. He cites several of his own publications in the paper, As far as I can judge, they are all critical of caffeine in pregnancy. Surely this puts him at risk of bias.
The best way to address such bias is to conduct a systematic review with precise methodology. Also, at least one other author should be involved in assessing suitability of the papers, and minimising bias.
Only English language papers are studied.
Only PubMed and Google Scholar are searched. No reference is made to other important databases such as CDSR, Medline, EMBASE and CINAHL.. There does not appear to have been any pre-specified eligibility criteria in assessing whether or not studies should be included in the review e.g. community based populations or pre defined study methods.
There is no attempt made to assess the quality of the studies used in writing the paper.
The search strategy appears vague.
The results in table 1 give odds ratio but there is no quantification of this. What we need is absolute risk with numbers needed to harm. If this figure cannot be calculated then we should be told and given the reasons why.
These limitations need to be acknowledged. For such an important topic potentially affecting so many vulnerable women, a more precise review and assessment of current evidence is warranted.
In this article, the authors follow a very ambitious objective: to refute the LDL central role in atherosclerosis paradigm. There is an ironic statement that quotes: if you point to the King, be sure not to leave him alive. Here I’m afraid this article leaves the King alive because the methodology chose had inferior quality of evidence in relation to a well-done metanalisys like –for example- the one which was published by the Cholesterol Treatment Trialist (CTT).
In order to the studies included in this selection there were some inconsistencies. First of all, the WOSCOPS trial and the AFCAPS/TexCAPS trial were used to analyze the effect of a reduction at least of 30% in LDL but these two pivotal articles showed a reduction of 20% and 25%, respectively. In fact, in the pilots’ study there were only 157 deaths from 6605 patients randomized so the study hadn’t enough statistical power to analyze the mortality endpoint. In the same direction, the selection of the SEAS study was controversial because in spite of achieves a 61% reduction in LDL, the population included hadn’t a clear indication of statin treatment in relation of ethical considerations, affecting the results in order to MACE and mortality. Also it was very polemical to include trials as SHARP or AURORA with patients on dialysis because we know this kind of treatment actives a lot of mechanisms of morbidity and mortality with independence of the LDL level. Other weak point is to analyze mortality taking in...
In this article, the authors follow a very ambitious objective: to refute the LDL central role in atherosclerosis paradigm. There is an ironic statement that quotes: if you point to the King, be sure not to leave him alive. Here I’m afraid this article leaves the King alive because the methodology chose had inferior quality of evidence in relation to a well-done metanalisys like –for example- the one which was published by the Cholesterol Treatment Trialist (CTT).
In order to the studies included in this selection there were some inconsistencies. First of all, the WOSCOPS trial and the AFCAPS/TexCAPS trial were used to analyze the effect of a reduction at least of 30% in LDL but these two pivotal articles showed a reduction of 20% and 25%, respectively. In fact, in the pilots’ study there were only 157 deaths from 6605 patients randomized so the study hadn’t enough statistical power to analyze the mortality endpoint. In the same direction, the selection of the SEAS study was controversial because in spite of achieves a 61% reduction in LDL, the population included hadn’t a clear indication of statin treatment in relation of ethical considerations, affecting the results in order to MACE and mortality. Also it was very polemical to include trials as SHARP or AURORA with patients on dialysis because we know this kind of treatment actives a lot of mechanisms of morbidity and mortality with independence of the LDL level. Other weak point is to analyze mortality taking into account studies that not official report it as ODYSSEY long Term and ODYSSEY COMBO I.
On the other hand, this article enlists essays in secondary prevention like FOURIER or IMPROVE-IT but it doesn’t include the HPS –with its huge statistical weight- or PROSPER –which achieves minor coronary death in elderly patients- or PROVE-IT or TNT. This situation looks like a whimsical selection without a solid support instead of a consistent piece of evidence.
I believe LDL central role in atherosclerosis is not quit questionable as the methodology used to calculate cardiovascular risk on primary prevention population or the residual risk in patients with prior heart disease. In my opinion, this would allow us to take the cardiovascular disease as the first cause of death of the world.
In this article, the authors follow a very ambitious objective: to refute the LDL central role in atherosclerosis paradigm. There is an ironic statement that quotes: if you point to the King, be sure not to leave him alive. Here I’m afraid this article leaves the King alive because the methodology chose had inferior quality of evidence in relation to a well-done metanalisys like –for example- the one which was published by the Cholesterol Treatment Trialist (CTT).
In order to the studies included in this selection there were some inconsistencies. First of all, the WOSCOPS trial and the AFCAPS/TexCAPS trial were used to analyze the effect of a reduction at least of 30% in LDL but these two pivotal articles showed a reduction of 20% and 25%, respectively. In fact, in the pilots’ study there were only 157 deaths from 6605 patients randomized so the study hadn’t enough statistical power to analyze the mortality endpoint. In the same direction, the selection of the SEAS study was controversial because in spite of achieves a 61% reduction in LDL, the population included hadn’t a clear indication of statin treatment in relation of ethical considerations, affecting the results in order to MACE and mortality. Also it was very polemical to include trials as SHARP or AURORA with patients on dialysis because we know this kind of treatment actives a lot of mechanisms of morbidity and mortality with independence of the LDL level. Other weak point is to analyze mortality taking in...
In this article, the authors follow a very ambitious objective: to refute the LDL central role in atherosclerosis paradigm. There is an ironic statement that quotes: if you point to the King, be sure not to leave him alive. Here I’m afraid this article leaves the King alive because the methodology chose had inferior quality of evidence in relation to a well-done metanalisys like –for example- the one which was published by the Cholesterol Treatment Trialist (CTT).
In order to the studies included in this selection there were some inconsistencies. First of all, the WOSCOPS trial and the AFCAPS/TexCAPS trial were used to analyze the effect of a reduction at least of 30% in LDL but these two pivotal articles showed a reduction of 20% and 25%, respectively. In fact, in the pilots’ study there were only 157 deaths from 6605 patients randomized so the study hadn’t enough statistical power to analyze the mortality endpoint. In the same direction, the selection of the SEAS study was controversial because in spite of achieves a 61% reduction in LDL, the population included hadn’t a clear indication of statin treatment in relation of ethical considerations, affecting the results in order to MACE and mortality. Also it was very polemical to include trials as SHARP or AURORA with patients on dialysis because we know this kind of treatment actives a lot of mechanisms of morbidity and mortality with independence of the LDL level. Other weak point is to analyze mortality taking into account studies that not official report it as ODYSSEY long Term and ODYSSEY COMBO I.
On the other hand, this article enlists essays in secondary prevention like FOURIER or IMPROVE-IT but it doesn’t include the HPS –with its huge statistical weight- or PROSPER –which achieves minor coronary death in elderly patients- or PROVE-IT or TNT. This situation looks like a whimsical selection without a solid support instead of a consistent piece of evidence.
I believe LDL central role in atherosclerosis is not quit questionable as the methodology used to calculate cardiovascular risk on primary prevention population or the residual risk in patients with prior heart disease. In my opinion, this would allow us to take the cardiovascular disease as the first cause of death of the world.
I read with interest the latest evidence for honey and treatment of coughs which was also reported widely in the national press (1). Honey has been shown in laboratory in vitro studies to inhibit bacterial growth including Helicobacter pylori linked with dyspepsia and gastritis (2, 3). Concentrations between 10-20% honey has been shown to be effective against both Gram negative and Gram positive bacteria (3). My late father Professor MNH Chowdhury, a clinical bacteriologist, researched this in the 1990s and advocated Manuka honey especially for its healing and antibacterIal properties. Interestingly, the in vitro findings showed some isolates were resistant to various antimicrobial agents but honey inhibited these organisms also (3). Secondary bacterial infections may respond to this simple remedy after primary viral coughs and colds and need further clinical study.
References
1. Abuelgasim H, Albury C, Lee J. Effectiveness of honey for symptomatic relief in upper respiratory tract infections: a systematic review and meta-analysis. BMJ Evidence Based Med 2020, 18 Aug online; bmjebm-2020-111336.
2. Rashed RS, Ayoola EA, Mofleh IA, Chowdhury MNH, Mahmood K, Faleh FZ. Helicobacter pylori and dyspepsia in an Arab population. Trop Geogr Med 1992; 44(4), 304-7.
3. Ali AT, Chowdhury MNH, al Humayyad MS. Inhibitory effect of natural honey on Helicobacter pylori. Trop Gastroenterol 1991; 12(3), 139-43.
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
Show Morea) 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...
Usman et al (1) write that only one of the 18 studies of COVID-19 patients they included in their review of the Smoker's Paradox reported that "the prevalence of smokers resembles that of the general population."
But this study--by Richardson et al in New York City (2)--actually only reported the prevalence of "never smokers" at 84.4%. It did not distinguish between current and former smokers among the remaining 15.6%, however, so Usman et al should have marked this combined result with an asterisk in their Table 1. Far from resembling the general population, the 15.6% combined rate is less than half the 34% expected in USA, where approximately 14% are current and 20% former smokers. With this correction, all 18 studies support the Smoker’s Paradox, which belies the authors’ conclusion that a “protective effect should NOT be inferred” [emphasis added].
The protective effect is clearly real and further supported by the largest study of COVID-19 to date (n=7,162) with data on smoking status (3), which Usman et al did not include in their review. Current smokers in this CDC study comprised just 1.3% of all the COVID-19 patients seeking care from US hospitals in 50 states and Washington DC, 1.2% of those treated as outpatients, and 1.1% of those treated in intensive care units.
Usman et al also did not mention the compound most likely responsible for the protective effects of smoking against respiratory infections, which...
Show MoreDear Editor,
Show MoreRecent literature suggested increased risk of severe COVID-19 in smokers which also got affirmation from World Health Organization (WHO) [1, 2]. However, original peer reviewed research which explained pathophysiological basis of the enhanced COVID-19 severity in smokers is currently scarce. Increased expression of SARS-CoV-2 cell entry receptor ACE2 in respiratory tract and lung tissue of smokers unraveled from analysis of gene expression data was used to predict higher chances of SARS-CoV-2 infection but that failed to explain enhanced COVID-19 severity [3]. Few authors have suggested that increased risk of severe complications and higher mortality rate in infected smokers may be due to host-specific factors like weakening of respiratory health and immunity caused by chronic smoking [4]. However, none of the virus-related factors which can be responsible for the COVID-19 severity in smokers has been reported until date. Based on the recent research updates on SARS-CoV-2 specific virulence in host cells, we propose a plausible mechanism which associates smoking with increased severity of COVID-19.
Apart from a cell surface entry receptor, coronaviruses require furin (a host protease) mediated cleavage of their spike (S) protein for successful invasion of the host cell. SARS-CoV-2, a member of the genus betacoronaviruses, has evolved a unique furin protease S1/S2 cleavage site, which is absent in other family members, including SARS-CoV-1 [5]. Rec...
First available online on August 18, 2020 in BMJ Evidence-Based Medicine, Aronson and Ferner (1) concluded that women using hormonal contraceptives cannot rely on their contraceptive method if they take a short course of non-enzyme inducing antibiotics based on Yellow Card reports to the UK’s Medicines and Healthcare products Regulatory Agency.
Show MoreWe believe that there are fundamental scientific issues and limitations with this study not adequately addressed by the authors. First, Yellow Card reports require provider reporting of an unintended pregnancy, which the authors acknowledge are subject to reporting bias. As the authors also acknowledge, many healthcare providers suspect there are drug-drug interactions between hormonal contraception and all antibiotics, despite the lack of definitive evidence (1). Therefore, there already exists a bias among providers that they would suspect and report an unintended pregnancy attributed to a drug-drug interaction among women taking antibiotics. The medications in each group are also not equivalent and bias the sample. For example, in the antibiotic group, metronidazole and nitrofurantoin are more commonly used in younger reproductive-aged and sexually active women (2,3), the population at highest risk of unintended pregnancies (4). In comparison, the control group includes such medications as propranolol and theophylline, which are used for treatment of cardiac and respiratory conditions more common among older women (5,6), wi...
In my daily practice that is limited, I've been allowing my patients to drink two cups of coffee a day, although they tend to be restrictive when applying my advice. Most of them are healthy women in their 30s. Whenever they've had a bad result, it has been attributed to other causes. When reading your impeccable research work, I've missed some comment on the clinical relevance of certain outcomes as a minor change in birth weight; moreover, aging or prior medical history may act as confounders of negative pregnancy outcomes. I appreciate your effort very much, but I consider the change of medical recommendations requires a more in-depth assessment, by means of one or more randomized clinical trials. Let's bear in mind than in my home country, Spain, temperatures in summer may be unbearable if you are an active working mother-to-be. And, definitely, our medical role is to give evidence-based solutions and avoid changing our pieces of advice every couple of years.
‘There is no safe level of caffeine intake in pregnancy’. That is the conclusion of this ‘narrative review’ of caffeine safety in pregnancy (BMJ Evidence Based Medicine, Open Access) which a patient brought to my attention very recently after hearing about it on the mainstream media. I felt that it requires clarification to avoid concern amongst the general public and those unable to analyse and critically appraise the literature.
The single author concluded that, after finding 48 studies (37 observational studies and 11 meta-analyses), caffeine intake in pregnancy significantly increases the risk of miscarriage, stillbirth, low birth weight, childhood leukaemia and childhood overweight/obesity. The author then goes on to recommend that all worldwide guidelines (including American, UK and Australian) stating the safety of caffeine in doses<200mg/day (approximately 2 cups of coffee) should be revised to say ‘there is no safe level of caffeine in pregnancy’.
However, there is no need to panic, which appears to be the response of the mainstream media and patients from the general population. Very soon after publication, this paper was picked up by several news outlets including CNN, The Guardian and also on a number of social media streams. Women were being told not to drink coffee in pregnancy the same way they were being told not to drink alochol.
This paper is far from as conclusive as it tries to make the reader believe, but serves as a good exampl...
Show MoreEditor,
I welcome this publication with it's focus on a potentially important cause of adverse pregnancy outcomes.
This study has several methodological faults that need to be declared and addressed.
The study's single author has written extensively on this topic over the last 29 years. He cites several of his own publications in the paper, As far as I can judge, they are all critical of caffeine in pregnancy. Surely this puts him at risk of bias.
The best way to address such bias is to conduct a systematic review with precise methodology. Also, at least one other author should be involved in assessing suitability of the papers, and minimising bias.
Only English language papers are studied.
Only PubMed and Google Scholar are searched. No reference is made to other important databases such as CDSR, Medline, EMBASE and CINAHL.. There does not appear to have been any pre-specified eligibility criteria in assessing whether or not studies should be included in the review e.g. community based populations or pre defined study methods.
There is no attempt made to assess the quality of the studies used in writing the paper.
The search strategy appears vague.
The results in table 1 give odds ratio but there is no quantification of this. What we need is absolute risk with numbers needed to harm. If this figure cannot be calculated then we should be told and given the reasons why.
These limitations need to be ackno...
Show MoreIn this article, the authors follow a very ambitious objective: to refute the LDL central role in atherosclerosis paradigm. There is an ironic statement that quotes: if you point to the King, be sure not to leave him alive. Here I’m afraid this article leaves the King alive because the methodology chose had inferior quality of evidence in relation to a well-done metanalisys like –for example- the one which was published by the Cholesterol Treatment Trialist (CTT).
Show MoreIn order to the studies included in this selection there were some inconsistencies. First of all, the WOSCOPS trial and the AFCAPS/TexCAPS trial were used to analyze the effect of a reduction at least of 30% in LDL but these two pivotal articles showed a reduction of 20% and 25%, respectively. In fact, in the pilots’ study there were only 157 deaths from 6605 patients randomized so the study hadn’t enough statistical power to analyze the mortality endpoint. In the same direction, the selection of the SEAS study was controversial because in spite of achieves a 61% reduction in LDL, the population included hadn’t a clear indication of statin treatment in relation of ethical considerations, affecting the results in order to MACE and mortality. Also it was very polemical to include trials as SHARP or AURORA with patients on dialysis because we know this kind of treatment actives a lot of mechanisms of morbidity and mortality with independence of the LDL level. Other weak point is to analyze mortality taking in...
In this article, the authors follow a very ambitious objective: to refute the LDL central role in atherosclerosis paradigm. There is an ironic statement that quotes: if you point to the King, be sure not to leave him alive. Here I’m afraid this article leaves the King alive because the methodology chose had inferior quality of evidence in relation to a well-done metanalisys like –for example- the one which was published by the Cholesterol Treatment Trialist (CTT).
Show MoreIn order to the studies included in this selection there were some inconsistencies. First of all, the WOSCOPS trial and the AFCAPS/TexCAPS trial were used to analyze the effect of a reduction at least of 30% in LDL but these two pivotal articles showed a reduction of 20% and 25%, respectively. In fact, in the pilots’ study there were only 157 deaths from 6605 patients randomized so the study hadn’t enough statistical power to analyze the mortality endpoint. In the same direction, the selection of the SEAS study was controversial because in spite of achieves a 61% reduction in LDL, the population included hadn’t a clear indication of statin treatment in relation of ethical considerations, affecting the results in order to MACE and mortality. Also it was very polemical to include trials as SHARP or AURORA with patients on dialysis because we know this kind of treatment actives a lot of mechanisms of morbidity and mortality with independence of the LDL level. Other weak point is to analyze mortality taking in...
I read with interest the latest evidence for honey and treatment of coughs which was also reported widely in the national press (1). Honey has been shown in laboratory in vitro studies to inhibit bacterial growth including Helicobacter pylori linked with dyspepsia and gastritis (2, 3). Concentrations between 10-20% honey has been shown to be effective against both Gram negative and Gram positive bacteria (3). My late father Professor MNH Chowdhury, a clinical bacteriologist, researched this in the 1990s and advocated Manuka honey especially for its healing and antibacterIal properties. Interestingly, the in vitro findings showed some isolates were resistant to various antimicrobial agents but honey inhibited these organisms also (3). Secondary bacterial infections may respond to this simple remedy after primary viral coughs and colds and need further clinical study.
References
1. Abuelgasim H, Albury C, Lee J. Effectiveness of honey for symptomatic relief in upper respiratory tract infections: a systematic review and meta-analysis. BMJ Evidence Based Med 2020, 18 Aug online; bmjebm-2020-111336.
2. Rashed RS, Ayoola EA, Mofleh IA, Chowdhury MNH, Mahmood K, Faleh FZ. Helicobacter pylori and dyspepsia in an Arab population. Trop Geogr Med 1992; 44(4), 304-7.
3. Ali AT, Chowdhury MNH, al Humayyad MS. Inhibitory effect of natural honey on Helicobacter pylori. Trop Gastroenterol 1991; 12(3), 139-43.
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