published between 2014 and 2017
We thank Mr/Ms Lin for the comments regarding our recent report (Long et al., 2017). We updated a meta-analysis on the association of smoking with NPC risk.
We agree with Mr/Ms Lin that Lin rightly stated that his/her paper used 'mortality' as the outcome, but the authors reported 'incidence' in the meta-analysis. We have to point out that we did include some valuable articles including Lin’s regarding the mortality or morbidity of NPC to make the review more comprehensive. However, we excluded these in the summary statistics of NPC incidence. For example, we did not Include Lin’s data in Figure 2.
We agree with Lin in that a meta-analysis of individual participant data (IPD) is needed to clarify the association between smoking and NPC. However, we do not think it is so called “a gold standard”. Instead, we recommend a novel Mendelian randomization analysis (MRA) approach. Using a gene-environment interaction and pathway analysis, we designed MRA to clarify the causal role of environmental exposures such as cigarette smoking in carcinogenesis (Fu et al 2012), because it is always difficult to address or clarify causal-effects by observational studies. We have used this strategy and clarified the causal role of red meat (Fu et al 2012) and cigarette smoking (Fu et al 2013) in pathogenesis of colorectal polyps, the precursors of colorectal cancer. This strategy was highlighted and orally presented in AACR annual meeting 2012 (...
We agree with Lin in that a meta-analysis of individual participant data (IPD) is needed to clarify the association between smoking and NPC. However, we do not think it is so called “a gold standard”. Instead, we recommend a novel Mendelian randomization analysis (MRA) approach. Using a gene-environment interaction and pathway analysis, we designed MRA to clarify the causal role of environmental exposures such as cigarette smoking in carcinogenesis (Fu et al 2012), because it is always difficult to address or clarify causal-effects by observational studies. We have used this strategy and clarified the causal role of red meat (Fu et al 2012) and cigarette smoking (Fu et al 2013) in pathogenesis of colorectal polyps, the precursors of colorectal cancer. This strategy was highlighted and orally presented in AACR annual meeting 2012 (http://cancerres.aacrjournals.org/cgi/content/short/72/8_MeetingAbstract...). Towards clarifying the causal role of smoking in NPC risk, further inputs and collaborations are welcome.
1. Long M, Fu ZM*, Lie Z, Li P. Cigarette smoking and the risk of nasopharyngeal carcinoma: a meta-analysis of epidemiological studies. BMJ Open 2017 Oct 5;7(10):e016582. doi: 10.1136/bmjopen-2017-016582.
2. Fu Z, Shrubsole MJ, Li GL, Smalley WE, Hein DW, Chen Z, Yu S, Cai QY, Ness RM, Zheng W. Using gene-environment interaction analyses to clarifying the association of colorectal polyp risk with well-done meat and heterocyclic amine exposure. Am J Clin Nutr, 2012 Nov;96(5):1119-28. PMID: 23015320.
3. Fu Z, Shrubsole MJ, Li GL, Smalley WE, Hein DW, Cai QY, Ness RM, Zheng W. Interaction of cigarette smoking and carcinogen-metabolizing polymorphisms in the risk of colorectal polyps. Carcinogenesis, 2013 Apr;34(4):779-86.
Thank you for an interesting paper. The authors claim that women were selected using a systematic random sampling technique. However, their report states that 'The first served pregnant woman and every second woman thereafter were invited to participate in the study until the required sample size was obtained.' This assumes that the women attended the clinic in random order. I they did attend in random order, then selecting every woman consecutively would produce an equally random sample. If there was some pattern to their attendance, then this is not a random sample. I think it would be more accurate to say that this was a convenience sample.
Thank you for raising this important point. Actually, the Poisson regression is usually used for count data with the variance equal to the mean. And Likert scale data is not suited to this statistic method directly. However, we standardized the scale and the data acquisition for the disability status within 30 days. We assumed that the standardized scores of each domain and summary score (from 0 to 100) as the count of disability status event in 30 days. For analysis the association between the variables of demographic data and standardized WHODAS 2.0 score, we choose the Poisson regression analysis, which could not be perfect for this study. (And the data is near to 1 even statistical significant) Therefore, we didn’t mention the outcome of table 3 in discussion part and conclusion part (merely, mentioned in result part). Our study finding is based on table 2 and we discussed this finding (lower disability status in the WHODAS 2.0 domains of getting along and social participation for patients with dementia with formal education compared with those without formal education) in discussion and conclusion part.
Thank you again for your precious suggestion. We agree that Multi-level IRT could be an appropriate way to analyze multiple Likert scales. The following studies of original Likert scales of WHODAS 2.0 will be analyzed as your suggestion and this could lead our study to be more convincing.
We appreciate this updated meta-analysis on smoking and NPC. However, one misinterpretation of our paper (Lin et al., 2015) was found.
The paper used 'mortality' as the outcome, but the authors reported 'incidence' in this paper.
The authors stated, the lack of individual participant data for adjustment of potential confounders. We agree that as a gold standard, a meta-analysis of individual participant data is needed to clarify the association between smoking and NPC.
There is considerable debate going on questioning the practical usefulness of a priori power calculations suggesting that “underpowered” studies are not unethical and that little scientific projection would be still better than no projection at all [1-4]. Some authors argue that “being underpowered is unethical” is a “widespread misconception which is only plausible when presented in vague, qualitative terms but does not hold when examined in detail” [1, 2]. Further review of the arguments reveals that the crucial assumptions implied in the reasoning do not reflect actual scientific practice. The main theoretical arguments assume a perfect “frequentist world” that may allow substitution of one big trial by a corresponding number of small trials that would, once being aggregated in a formal evidence synthesis i.e. meta-analysis, cumulate the same information as the big one [2, 4]. If the individual studies are non-representative samples of the target population, the practical value of estimating a pooled effect that is a weighted average of potentially disparate effects in different subpopulations is questionable.
A widely considered answer to the threat of effect heterogeneity in meta-analyses are random-effect confidence intervals that are often assumed to better reflect variation in the effects across subpopulations than fixed-effects confidence intervals. However, while such intervals offer a valid solution to inference regarding the average effect across all c...
A widely considered answer to the threat of effect heterogeneity in meta-analyses are random-effect confidence intervals that are often assumed to better reflect variation in the effects across subpopulations than fixed-effects confidence intervals. However, while such intervals offer a valid solution to inference regarding the average effect across all contributing effects, they continue to suffer from the principal limitations of effect estimates that are based on non-representative samples: the location and width of these confidence intervals will ultimately depend on the representation of subpopulations and therefore on the selection mechanisms inherent to the data.
While these are well-known and widely debated limitations of most sample-based research studies, another fundamental interpretational issue applies to confidence intervals: they refer to the mean (or average) effect across subpopulations. In the context of meta-analyses, with a large enough number of studies, either random or fixed effects confidence intervals will not cover the actual range of observed study-specific effect estimates. In other words, the intervals are providing a precise estimate of a parameter that actually does not exist, as it represents a weighted average of an underlying set of parameters in homogenous subpopulations.
In a recent plea for routinely presenting prediction intervals in meta-analysis , InHout et al. promote reporting prediction intervals, in addition to confidence intervals . Prediction intervals reflect the variation in treatment or exposure effects over different settings, and allow to infer on what effect is to be expected in future individuals, such as a patient that a clinician is interested to treat. In contrast to confidence intervals, prediction intervals do not shrink to zero width if the sample size largely increases but cover a prespecified range of expected effects in the underlying population. The authors conclude that prediction intervals should be routinely reported to allow for more informative inferences in meta-analyses.
We suggest that prediction intervals are not only meaningful in the context of meta-analyses, but, as implied by the generally applicable concept of variance decomposition , may be in a very similar way relevant to reporting individual studies or trials.
The interest in subgroup analyses in individual studies is often not properly addressed at the analysis stage due to a general claim of “lack of power” that would arise in stratified analyses or modelling approaches including interaction terms. As a result, a single point estimate is often reported along with a confidence intervals that implies homogeneity of the effect across all known subgroups. Such subgroups do, in our point of view, constitute subpopulations similar to subpopulations (studies) in meta-analyses. We therefore question, why should we not consider reporting prediction intervals for single study effect estimates based on pre-specified subgroups such as strata used for randomization or purposive sampling in the context of clinical trials?
1. Bacchetti P, McCulloch CE, Segal MR. Being ‘underpowered’ does not make a study unethical. . Statistics in Medicine 2011; 30:2785–2792.
2. Bacchetti P, Wolf LE, Segal MR, McCulloch CE. Ethics and sample size. American Journal of Epidemiology 2005; 161:105–110.
3. Bacchetti P, McCulloch CE, Segal MR. Simple, defensible sample sizes based on cost efficiency. Biometrics 2008; 64:577–585.
4. Edwards SJL, Lilford RJ, Braunholtz D, Jackson J. Why “underpowered” trials are not necessarily unethical. Lancet 1997; 350:804–807.
5. IntHout J, Ioannidis JP, Rovers MM, Goeman JJ. Plea for routinely presenting prediction intervals in meta-analysis. BMJ open. 2016 Jul 1;6(7):e010247.
6. Weiss NA. A course in probability. Addison-Wesley; 2006.
As postpartum hemorrhage (PPH) researchers, and leaders in education and care of maternal health emergencies, from the United States, UK, Canada, India, Peru, Honduras, Zambia, India, Kenya, Tanzania, Colombia and Nepal, we read the Dumont et al paper with great interest. We would like to share our review:
The most fundamental flaw of this paper is that the authors confuse an intention-to-treat study of a clinical pathway of interventions and behaviors, with the efficacy of a device. These are two very different research questions. In order to test the latter via a randomized controlled trial (RCT) the two groups would need to be the similar and subjects that did not even receive the device (or received it in desperation two hours after the diagnosis of uncontrolled PPH) certainly could not be included in the intervention group. Thus, this study attempts to test intention-to-treat, not the efficacy of the uterine balloon tamponade (UBT) device.
The second most obvious flaw is that degrees of illness are not accounted for. Clinically defined "uncontrolled PPH" is in no way a homogeneous group. For example, someone that has been referred in and is moribund from their advanced shock is an entirely different subject than someone who has mild uncontrolled PPH. Since this is not controlled for, these two groups are likely incomparable.
Even taking into account the two issues described above, the two groups are different and heavily favor the non-...
Even taking into account the two issues described above, the two groups are different and heavily favor the non-intervention group. For example, in the intervention group the following were considerably worse than in the non-intervention group: late uterotonics (54% vs 37%) and retained products of conception/placenta (19% vs 10%). Additionally, UBTs were placed more than 30 minutes after diagnosis of uncontrolled PPH in 58% of cases
Therefore, while this study truly does not test the UBT device, what it does do is tell us that the care providers were not able to provide quality care to women defined as having uncontrolled PPH, despite being within the framework of a study that encouraged best practice. This is indeed extremely important. This study adds to the growing literature describing that performance of health care providers may often be inconsistent and suboptimal in maternal health emergencies, and, that these poor practices may contribute to the flawed nature of RCTs in maternal health interventions.
Prof Burke, Prof Arulkumaran, Prof. Rogo, Dr. Manasyn, Susana Ku, RMW, Monica Oguttu, RNMW, Dr. Thapa, Prof Ochoa, Prof. Tarimo, Dr. Eckardt, Dr. Suarez and Dr. Garg,
We have read the study conducted by Diniz et al. on the possible association between mammography and breast cancer-related mortality in the state of São Paulo, Brazil with the greatest of care. Despite the detailed statistical analysis, the ecological study design implies limitations to the hypothesis generated, as pointed out by the authors themselves (1). In our opinion, both the authors’ main conclusion and the assumed association of cause and effect are inappropriate.
The factors associated with the incidence of breast cancer in Brazil and its resulting mortality have recently been evaluated in different studies (2-4). Mortality rates have been found to vary as a function of geospatial location (rural areas versus urban centers)(4). In addition, the reduction encountered in mortality was associated with the regions in which the human development index (HDI) was higher. On the other hand, the highest mortality rates have been found to occur in the states with the highest HDI (5). Diniz et al. and many other investigators have mentioned that a higher incidence of breast cancer occurs among more affluent women living in urban areas and in large cities (1,5). In this respect, we are certain that mortality is also related to the incidence of the disease; hence, the higher the incidence, the greater the resulting mortality will be. Conversely, women who do not have breast cancer will obviously not die from the disease.
Therefore, we believe t...
Therefore, we believe that the study conducted by Diniz et al. should be interpreted in another manner. According to their report, breast cancer-related mortality was associated with three characteristics of the more affluent female population in Brazil: healthcare within the private healthcare system, nulliparity, and access to mammography (1). Nevertheless, the women with greatest access to mammography are those with better socioeconomic conditions living in urban areas and for this reason are more likely to develop breast cancer and, consequently, to die from this disease.
The authors take advantage of the results obtained to criticize mammography screening. In fact, screening programs must reach at least 70% of the target population to be considered effective. In 2016, the coverage provided by mammography screening within the Brazilian National Health Service (Sístema Único de Saúde - SUS) reached only 24% of the female population of 50 to 69 years of age. This percentage almost doubles within the supplementary healthcare system (6,7), and that fact also permits a critical analysis to be made in relation to the results obtained by Diniz et al. (1). In other population-based studies, improved access to healthcare and an increase in the number of mammograms performed was found to be associated with a considerable reduction in cases of breast cancer diagnosed at an advanced stage in some regions (7-9). When well conducted, mammography screening can reduce mortality by approximately 30% (10).
In terms of radiological protection, mammography screening is justifiable if the imaging procedures performed are of excellent quality and conducted using the lowest possible dose of radiation (11,12). Diniz et al. concluded that the number of cases of radiation-induced cancer caused by the ionizing radiation from imaging could be increasing the mortality rate (1). This association is wrong, since it would be necessary to take the dose at which the imaging procedure is performed into consideration, together with other factors, to enable the number of cases of radiation-induced cancer in a population to be calculated (13). Corrêa et al. found that the number of imaging procedures performed was not associated with the number of breast cancer deaths induced by women’s exposure to radiation and concluded that the final magnitude of the risk was exclusively determined by the dose of radiation emitted by the mammography equipment (13).
In the study conducted by Corrêa et al., the likelihood of developing a radiation-induced cancer as a result of mammography was found to be 0.2 per 100,000 women. Furthermore, the probability of death at 85 years of age as a result of the accumulated radiation dose to which a woman would be exposed at imaging procedures conducted every two years was estimated at 0.18 per 100,000 women annually. Therefore, the risk of dying from radiation-induced cancer is much lower than the risk associated with other factors that could result in death, including not undergoing imaging for the early detection of breast cancer and thus being diagnosed at an advanced stage (13,14). In a recent study, women receiving care within the private healthcare system were found to be half as likely to have advanced lesions at diagnosis, reflected in an increase in survival of approximately 10% in relation to the women treated within the Brazilian National Healthcare Service (SUS) (15). These data also conflict with those reported by Diniz et al. (1).
In the statistical analysis, Diniz et al. selected and analyzed an expressive set of explanatory variables. They also performed multiple regression analyses and applied the Akaike Information Criterion (AIC), which estimates the model with the best fit, to the set of resulting models (1). Nevertheless, application of the AIC does not judge whether the best-fit model found is actually satisfactory, bearing in mind that all the models could be inadequate. The final fitted model used by the authors contains the following variables: the mammography ratio, the percentage of women with private healthcare and the proportion of women of childbearing age who did not have children. Therefore, many important variables were largely ignored in the analysis, including the gross domestic product, human development index, and income, among others.
Figure 1 in the paper merits further scrutiny, together with charts on the human development index, gross domestic product and income. Despite the availability of computer software programs such as Geographically Weighted Regression (GWR) (16), the authors elected to use the Global Moran’s Index, even in the presence of spatial clusters from the municipalities with higher and lower mortality rates as shown in Figure 1. Apparently, these clusters occur in metropolitan regions where socioeconomic factors are high but whose population is larger and exposed to greater levels of pollution, stress and anxiety. Therefore, the Local Moran’s Index rather than the Global Moran’s Index should be applied to this map (17). In this respect, we believe that the analysis of the results was inadequate, since the study’s findings were not discussed in relation to the social, economic and environmental factors associated with the occurrence of mortality in the state of São Paulo, Brazil. Finally, a critical analysis should be conducted with respect to the data collection and registry of mammograms performed within the Brazilian National Health Service (SUS). Individuals who have to travel to another municipality to undergo mammography (18), sometimes within the private healthcare system, and the bias in the mammography registries caused by discrepancies in the public funding of the exams should be emphasized.
Based on the aforementioned considerations, we conclude that the study conducted by Diniz et al., although contributing with a fairly important analysis, fails to reach an adequate conclusion (1). According to our analysis, breast cancer-related mortality is associated with factors linked to social and medical development in the state of São Paulo.
Rosemar Macedo Sousa Rahal
Rosangela da Silveira Corrêa
Danielle Cristina Netto Rodrigues
Nilson Clementino Ferreira
Noley Vicente Ribeiro
Leonardo Ribeiro Soares
1. Diniz CSG, Pellini ACG, Ribeiro AG, et al. Breast cancer mortality and associated factors in São Paulo State, Brazil: an ecological analysis. BMJ Open 2017;7(8):e016395.
2. Cecilio AP, Takakura ET, Jumes JJ, et al. Breast cancer in Brazil: epidemiology and treatment challenges. Breast Cancer (Dove Med Press) 2015;7:43-9.
3. Gonzaga CM, Freitas-Junior R, Curado MP, et al. Temporal trends in female breast cancer mortality in Brazil and correlations with social inequalities: ecological time-series study. BMC Public Health 2015;15:96.
4. Gonzaga CM, Freitas-Junior R, Souza MR, et al. Disparities in female breast cancer mortality rates between urban centers and rural areas of Brazil: ecological time-series study. Breast 2014;23(2):180-7.
5. Liedke PER, Finkelstein DM, Szymonifka J, et al. Outcomes of Breast Cancer in Brazil Related to Health Care Coverage: A Retrospective Cohort Study. Cancer Epidemiol Biomarkers Prev 2014; 23:126-33.
6. Freitas-Junior R, Rodrigues DCN, Corrêa RS, et al. Contribution of the Unified Health Care System to mammography screening in Brazil, 2013. Radiol Bras 2016; 49(5): 305-10.
7. Smith RA, Duffy SW, Gabe R, et al. The randomized trails of breast cancer screening: what have we learned? Radiol Clin North Am 2004; 42:793-806.
8. Martins E, Freitas-Junior R, Curado MP, et al. [Temporal evolution of breast cancer stages in a population-based cancer registry in the Brazilian central region]. Rev Bras Ginecol Obstet 2009;31(5):219-23.
9. Nunes RD, Martins E, Freitas-Junior R, et al. Descriptive study of breast cancer cases in Goiânia between 1989 and 2003. Rev Col Bras Cir 2011;38(4):212-6.
10. Corrêa R. da S, Freitas-Júnior R, Peixoto JE, et al. [Estimated mammogram coverage in Goiás State, Brazil]. Cad Saude Publica 2011;27(9):1757-67.
11. Berrington de González A, Reeves G. Mammographic screening before age 50 years in the UK: comparison of the radiation risks with the mortality benefits. Br J Cancer 2005;93:590-6.
12. Corrêa R da S, Peixoto JE, Ferreira RDS, et al. Risco de câncer radioinduzido em rastreamento mamográfico. Rio de Janeiro, RJ, Brazil: IX Latin American IRPA Regional Congress on Radiation Protection and Safety - IRPA 2013, 2013. http://www.iaea.org/inis/collection/NCLCollectionStore/_Public/45/071/45...
13. Yaffe MJ, Mainprize JG. Risk of radiation-induced breast cancer from mammographic screening. Radiology 2011;258:98-105.
14. Young KC, Faulkner K, Wall B, et al. UK National Health Service Breast Screening Programme (NHSBSP). Review of radiation risk in breast screening. NHSBSP Publication no. 54, 2003.
15. Anselin L. Exploring Spatial Data with GeoDATM: A Workbook. Center for Spatially Integrated Social Science, 2005.
16. Wheeler D, Tiefelsdorf M. Multicollinearity and correlation among local regression coefficients in geographically weighted regression. J Geog Syst 2005;7:161-87.
17. Henley SJ, Anderson RN, Thomas CC, Massetti GM, Peaker B, Richardson LC. Invasive Cancer Incidence, 2004-2013, and Deaths, 2006-2015, in Nonmetropolitan and Metropolitan Counties - United States. MMWR Surveill Summ 2017;66(14):1-13.
18. Vieira RADC, Formenton A, Bertolini SR. Breast cancer screening in Brazil. Barriers related to the health system. Rev Assoc Med Bras (1992). 2017;63:466-74.
Please see my article with the above name, published in the New Zealand Medical Journal, which used the Caerphilly data. This has not been mentioned elsewhere, presumably because of its obscure site. There was no relationship at all between cholesterol and heart attacks and only 4% of the variance was associated with strokes. NZ Med. J. 2012, 125, 1364.
This study asks the important question, what proportion of systematic reviews searched for and made use of unpublished data? However, an important follow-up question remains to be addressed: Among those cases in which unpublished data was used, how was it used? Unpublished data can of course address study publication bias, ie. data from unpublished studies can be simply added to data obtained from the published literature. However, unpublished data can also address outcome reporting bias,[1-3] ie. a trial publication conveys that the intervention is safe and/or effective while unpublished data on the same trial tell a different story. For example, in a study of 74 industry-sponsored antidepressants trials, in addition to 23 (31%) unpublished trials, we found 11 (15%) trials with outcome reporting bias. If we had corrected for the former while ignoring the latter, we would have obtained an effect size estimate that was still inflated. Returning to the current study, an informative follow-up would be to look within the cohort of systematic reviews that made use of unpublished data and determine how many used it to verify the published results.
1 Kirkham JJ, Dwan KM, Altman DG, et al. The impact of outcome reporting bias in randomised controlled trials on a cohort of systematic reviews. BMJ 2010;340:c365.
2 Chan A-W, Altman DG. Identifying outcome reporting bias in randomised trials on PubMed: review of publications and survey of author...
2 Chan A-W, Altman DG. Identifying outcome reporting bias in randomised trials on PubMed: review of publications and survey of authors. BMJ 2005;330:753. doi:10.1136/bmj.38356.424606.8F
3 Chan A-W, Hróbjartsson A, Haahr MT, et al. Empirical evidence for selective reporting of outcomes in randomized trials: comparison of protocols to published articles. JAMA 2004;291:2457–65. doi:10.1001/jama.291.20.2457
4 Turner EH, Matthews AM, Linardatos E, et al. Selective publication of antidepressant trials and its influence on apparent efficacy. N Engl J Med 2008;358:252–60. doi:10.1056/NEJMsa065779
5 Ziai H, Zhang R, Chan A-W, et al. Search for unpublished data by systematic reviewers: an audit. BMJ Open 2017;7:e017737. doi:10.1136/bmjopen-2017-017737
We thank Dr. Fowler and colleagues for taking the time to consider and comment on our BMJ Rapid Recommendation (1). They speculate on reasons why tenofovir and emtricitabine increased the risk of neonatal mortality and early preterm delivery in their trial (2) and then say that the current evidence does not support a recommendation for alternative NRTIs over a tenofovir-based antiretroviral therapy (ART) regimen. We do agree that most, but not all, of the evidence comes from a single study, which may have overestimated harm. Our systematic review attempted to generate the current best evidence, and is not definitive: it is moderate-to-low quality for key outcomes (3). However, we disagree with the implication that based on this evidence, most women would choose a tenofovir-based ART regimen.
The PROMISE authors suggest that results of the comparison between tenofovir-ART and AZT-ART are untrustworthy because the risk of neonatal death was lower in the AZT-ART arm in the earlier period 1 before the tenofovir-ART arm was introduced (2). However, the difference between the two time-periods in the AZT-ART arm could easily be explained by chance (neonatal mortality 1.4% in period 1 vs. 0.6% in period 2, p=0.39; very preterm delivery 3.4% in period 1 vs. 2.6% in period 2, p=0.60). Regardless, the only reliable comparison between tenofovir-ART and AZT-ART is during period 2 when randomisation to both AZT and tenofovir-based ART occurred. Despite these r...
The PROMISE authors suggest that results of the comparison between tenofovir-ART and AZT-ART are untrustworthy because the risk of neonatal death was lower in the AZT-ART arm in the earlier period 1 before the tenofovir-ART arm was introduced (2). However, the difference between the two time-periods in the AZT-ART arm could easily be explained by chance (neonatal mortality 1.4% in period 1 vs. 0.6% in period 2, p=0.39; very preterm delivery 3.4% in period 1 vs. 2.6% in period 2, p=0.60). Regardless, the only reliable comparison between tenofovir-ART and AZT-ART is during period 2 when randomisation to both AZT and tenofovir-based ART occurred. Despite these reservations, we performed sensitivity analyses that included data from the AZT-arm in period 1 before the tenofovir-ART arm was introduced (3). The increased risk of early preterm delivery and stillbirth with tenofovir/emtricitabine remained statistically significant and interpretation does not change when data from period 1 is included. Dr. Fowler and colleagues have also suggested that there may have been “some unknown confounder” wherein tenofovir-ART caused harm during period 2, but would not have been harmful to the participants in period 1 (2, 4). We consider this unlikely. Even if true, no such confounder has been identified and women faced with choosing an ART regimen will not know whether or not tenofovir-ART has the potential for harm in their case.
We agree that when tenofovir and emtricitabine are used in combination with lopinavir/ritonavir, it is possible that the risk is higher than with efavirenz; although it is unlikely that if tenofovir is indeed the ‘culprit’ medication, that there would be no risk at all when combined with efavirenz. Put another way, even if the risk of premature delivery and neonatal death is low with tenofovir/emtricitabine plus efavirenz, based on the available evidence, the risk with AZT/lamivudine plus efavirenz may be even lower.
We did not state that the pathophysiology of stillbirth and early neonatal death are the same. Perinatal mortality has long been a global standard outcome measure of maternal and perinatal healthcare (5) and is likely to be similarly important to women, thus our panel pre-specified that it was appropriate to combine them in our evidence summary.
We agree with their concern regarding the possibility that all combination ART regimens may increase the risk of prematurity (versus no ART or monotherapy), albeit this is uncertain and not the focus of this guidance. Given the unique physiology (and pathophysiologies) of pregnancy, the lack of an understood biological rationale at this stage should neither lead to a definitive conclusion nor reassurance. It remains possible that potential pharmacokinetic interactions, and failing or restoring immune systems are different in pregnancy. These are all good reasons to recognise that work from non-pregnant male and female adults cannot always be applied directly to pregnant women. Instead, these are strong justifications for further pregnancy-specific research. We believe that pregnant women (and their babies) should have an equitable standard of research evidence, and thus disagree that it is unlikely that there will be other randomised trials. It is imperative that further randomised trials are conducted. Regulatory authorities, and perhaps the WHO, have a responsibility to ensure that the appropriate studies are performed by the pharmaceutical industry to ensure that pregnant women are not disadvantaged.
Fowler et al. assert that the available observational evidence should provide reassurance to pregnant women. In this, we believe they are misguided. We reviewed the entirety of the observational evidence, including the single observational study that they cite (6); it cannot provide such assurance. First, even the highest quality observational studies are at high risk of residual confounding (7). Second, none of the studies controlled for all of the most important known confounders, including HIV disease status (CD4 count and viral load), socioeconomic status, and availability and quality of healthcare. Third, the studies were inconsistent with some showing harm with tenofovir and others benefit. Fourth, the results were imprecise with the confidence intervals including a magnitude of harm that almost all women would find important.
We strongly disagree with any implication that most women would be willing to risk the health of their child when other options exist. The decision about which vertical transmission strategy or combination ART regimen to use should rest squarely with each informed woman, based on her own values and preferences. This message was consistent from the linked systematic review on the values and preferences of women living with HIV (8), from the three women living with HIV on the guideline panel, as well as an associated opinion piece written by a woman living with HIV (9). Avoiding death in a newborn child is tremendously important to all or almost all women and even if the increased risk of stillbirth or neonatal mortality is extremely low with tenofovir/emtricitabine, almost all women would choose to use a different regimen. Unless future randomised trials show that tenofovir/emtricitabine is safe, we believe that most fully informed women would choose an alternative. Efforts should be made to share the best available evidence and empower women who are pregnant or might consider pregnancy to choose their medications for themselves rather than a ” one size fits all” approach to HIV treatment.
Reed A.C. Siemieniuk, Graham P. Taylor, Gordon H. Guyatt, Lyubov Lytvyn, Yaping Chang, Paul E. Alexander, Yung Lee, Thomas Agoritsas, Arnaud Merglen, Haresh Kirpalani, Susan Bewley
1. Siemieniuk RA, Lytuyn L, Ming JM et al. Antiretroviral therapy in pregnant women living with HIV: a clinical practice guideline. BMJ 2017;358:j3961.
2. Fowler MG, Qin M, Fiscus SA, et al. Benefits and risks of antiretroviral therapy for perinatal prevention. N Engl J Med 2016;375:1726-37.
3. Siemieniuk RA, Foroutan F, Mirza R et al. Antiretroviral therapy for pregnant women living with HIV or hepatitis B: a systematic review and meta-analysis. BMJ Open 207;7:e019022.
4. Peer review of Siemieniuk RA, Foroutan F, Mirza R et al. Antiretroviral therapy for pregnant women living with HIV or hepatitis B: a systematic review and meta-analysis. BMJ Open 207;7:e019022. Available at: http://bmjopen.bmj.com/content/bmjopen/7/9/e019022.reviewer-comments.pdf Accessed October 9, 2017.
5. World Health Organization. “Maternal and perinatal health.” http://www.who.int/maternal_child_adolescent/topics/maternal/maternal_pe... Accessed October 9, 2017.
6. Zash R, Jacobson DL, Diseko M, et al. Comparative Safety of Antiretroviral Treatment Regimens in Pregnancy. JAMA Pediatr. 2017 Oct 2;171(10):e172222.
7. Agoritsas T, Merglen A, Shah ND, O'Donnell M, Guyatt GH. Adjusted Analyses in Studies Addressing Therapy and Harm: Users' Guides to the Medical Literature. JAMA. 2017 Feb 21;317(7):748-759.
8. Lytvyn L, Siemieniuk RA, Dilmitis S, et al. Values and preferences of women living with HIV who are pregnant, postpartum or considering pregnancy on choice of antiretroviral therapy during pregnancy. BMJ Open. 2017 Sep 11;7(9):e019023.
9. Welbourn, A. WHO and the rights of women living with HIV. BMJ Opinion. Available at: http://blogs.bmj.com/bmj/2017/09/11/alice-welbourn-who-and-the-rights-of... Accessed October 9, 2017.