We appreciate the interest that Dr. Pedersen has shown in our paper, but he has apparently misunderstood some aspects of our analysis. In the analysis of the stillbirth data, we first described the dependence of log (rate) on calendar year by a straight line. Next, we allowed the slope to change from 2011 onwards (a so-called linear spline with a knot at 2011). This did not improve the fit significantly. This is the analysis reported in our paper. Besides we also tried to see if a change in intercept from 2011 onwards would lead to a significantly better fit. This was not the case. This latter model is the one that Dr. Pedersen considers, but this was not the one presented in our paper.
We are also concerned about Dr. Pedersen’s suggestion that we have been unresponsive to his questions. We can document at least 11 email correspondences and two face to face meetings with Dr. Pedersen to accommodate Dr. Pedersen’s wish for more information and discussion of our analyses. These mails and meetings have also included the Lead Professor of Dr. Pedersen’s department and a Professor in Biostatistics from Aarhus University. The Professor in Biostatistics has confirmed to all included in the meetings and in the additional emails that our analysis as well as our conclusions in the paper were valid.
Eva Rydahl, Eugene Declercq, Mette Juhl, Rikke Damkjær Maimburg
De Rubeis et al. conducted a systematic review to evaluate the effect of disasters, including pandemics, on cardiometabolic outcomes (1). Clinical outcomes were checked ≥1 month following the disaster. The effects of exposure to disaster during pregnancy/childhood and during adulthood were included, and increased cardiovascular disease incidence or mortality, diabetes and obesity were observed in each study. Although the biological mechanisms of the association might be complex, long-term effects of disasters on cardiometabolic health should be explored to elucidate prevention strategies against forthcoming disasters (2-4).
References
1. e Rubeis V, Lee J, Anwer MS, et al. Impact of disasters, including pandemics, on cardiometabolic outcomes across the life-course: a systematic review. BMJ Open. 2021;11(5):e047152.
2. Chua MWJ. Managing patients with obesity in the post COVID-19 world: Time to sharpen the saw. Obes Res Clin Pract. 2021;15:85-88.
3. Narita K, Hoshide S, Tsoi K, et al. Disaster hypertension and cardiovascular events in disaster and COVID-19 pandemic. J Clin Hypertens (Greenwich). 2021 ;23(3):575-583.
4. Burg MM, Soufer R. Post-traumatic Stress Disorder and Cardiovascular Disease. Curr Cardiol Rep. 2016;18(10):94
Dear Dr. Walid Al-Wali et al,
Thank you for interest in our work, particularly for your comments on the published protocol titled: Estimating the vaccine confidence levels among healthcare students and staff of a tertiary institution in South Africa.
As you rightly observed, and as stated in the article, the study population is healthcare students and staff of a tertiary institution in South Africa. In this particular setting (a medical campus) a significant number of medical students in their senior years as well as staff have direct dealings with, and exposure to patients in the adjacent teaching hospital as part of their studies and routine duties. These, therefore, were considered as part of the frontline healthcare workers that were prioritized for the receipt of the COVID 19 vaccines, the roll-out of which at the time of the design of our study, was imminent. One of the main aims of our study was to investigate the intention to receive a COVID 19 vaccine when one becomes available. This cogent reason makes the population described above ideal for our study.
Moreover, the selected study population is relevant to gaining some insight on the probable vaccine sentiments of future healthcare workers, identifying any issues of concern and planning how to mitigate them, and gauging how well they might likely advocate for vaccine acceptance. The representability of the current population views (though they are part of the larger population and possibly part...
Dear Dr. Walid Al-Wali et al,
Thank you for interest in our work, particularly for your comments on the published protocol titled: Estimating the vaccine confidence levels among healthcare students and staff of a tertiary institution in South Africa.
As you rightly observed, and as stated in the article, the study population is healthcare students and staff of a tertiary institution in South Africa. In this particular setting (a medical campus) a significant number of medical students in their senior years as well as staff have direct dealings with, and exposure to patients in the adjacent teaching hospital as part of their studies and routine duties. These, therefore, were considered as part of the frontline healthcare workers that were prioritized for the receipt of the COVID 19 vaccines, the roll-out of which at the time of the design of our study, was imminent. One of the main aims of our study was to investigate the intention to receive a COVID 19 vaccine when one becomes available. This cogent reason makes the population described above ideal for our study.
Moreover, the selected study population is relevant to gaining some insight on the probable vaccine sentiments of future healthcare workers, identifying any issues of concern and planning how to mitigate them, and gauging how well they might likely advocate for vaccine acceptance. The representability of the current population views (though they are part of the larger population and possibly participate in the ongoing conversations about vaccines and vaccination, especially COVID 19 vaccines and vaccination) by these future health care workers and their trainers was not the intention nor part of the expected outcome of this current study.
We do concede that there is a limit to the extent to which their views will reflect current feelings, attitudes, practices and gaps in knowledge when compared to that of the general public. However, we do not consider this to be a major issue, as the merits of the study far outweighs this limitation. Nonetheless, this limitation will be duly acknowledged in the full report of the study.
Admittedly, exploring what are the things that will make health care students and staff confident in a vaccine, be prepared to take it, recommend and administer it to the public is a worthwhile question to ask, but, that again, is outside the scope of this present study.
Finally, we also agree that the study population due to its peculiarity is an ideal group to interface with the public as their communication platform is relevant and may be far reaching than the ‘traditional’ means of communication.
Thank you once again for your interest in our work, and for constructively engaging with us.
Do be on the lookout for the detailed report of the study that is now in progress. We look forward to future interactions with you.
Thank you all, God bless you all
I would like to congratulate Hannah Dahlen and colleagues on their recent publication in BMJ Open (1), particularly with respect to their follow-up of longer-term outcomes for infants born following induction of labour between 37 and 41 completed weeks gestational age compared with women who had a spontaneous onset of labour.
Dahlen et al found that adverse maternal outcomes including caesarean section, instrumental birth, epidural use (potentially indicating a more painful and/or longer labour), episiotomy and post-partum haemorrhage were more common among women with an induced labour compared with women who went into spontaneous labour.
They list absence of an intention-to-treat analysis as a weakness in the study design, but go on to say, “the data sources have a good track record of accuracy, so we do not believe these errors are likely to be large, or that they would have significantly influenced the direction of effect of the outcomes.”
However, even if the data were perfectly accurate, the lack of intention-to-treat analysis causes a selection bias to an extent which makes it impossible to assess the impact of non-medically indicated induction of labour on maternal, neonatal, and child outcomes.
In a randomised trial of planned induction of labour at a given gestational age, an intention-to-treat analysis will include all randomised women, including those who went on to have a later medically indicated induction of labour. Similarly, in an o...
I would like to congratulate Hannah Dahlen and colleagues on their recent publication in BMJ Open (1), particularly with respect to their follow-up of longer-term outcomes for infants born following induction of labour between 37 and 41 completed weeks gestational age compared with women who had a spontaneous onset of labour.
Dahlen et al found that adverse maternal outcomes including caesarean section, instrumental birth, epidural use (potentially indicating a more painful and/or longer labour), episiotomy and post-partum haemorrhage were more common among women with an induced labour compared with women who went into spontaneous labour.
They list absence of an intention-to-treat analysis as a weakness in the study design, but go on to say, “the data sources have a good track record of accuracy, so we do not believe these errors are likely to be large, or that they would have significantly influenced the direction of effect of the outcomes.”
However, even if the data were perfectly accurate, the lack of intention-to-treat analysis causes a selection bias to an extent which makes it impossible to assess the impact of non-medically indicated induction of labour on maternal, neonatal, and child outcomes.
In a randomised trial of planned induction of labour at a given gestational age, an intention-to-treat analysis will include all randomised women, including those who went on to have a later medically indicated induction of labour. Similarly, in an observational study an intention-to-treat analysis will include women who go on to have a later induction of labour.
The study group (women who had an apparent non-medically indicated induction of labour) included women who would have had a medically indicated induction at a later gestational age. The control group (women who went into spontaneous labour) purposefully excluded this higher-risk group of women. Thus, we are not comparing like with like and medically indicated induction of labour is artificially made to appear to be associated with adverse outcomes.
This bias is well-recognised and is specific to studies about induction of labour.(2) It explains why observational studies which include only women in spontaneous labour in the comparison group show that induction of labour is associated with caesarean section,(2) whereas randomized controlled trials and observational studies such as the study published by Stock et al in BMJ(3) show the opposite.
Additionally, other biases may affect these observational studies, such as incorrect identification of truly non-medically indicated inductions of labour, and adjustment for confounders that may be on the causal pathway between induction of labour and adverse outcomes.
Thus, in my opinion, while Dahlen et al describe important population-based trends such as increasing rates of apparent non-medical indications of labour, the findings of their comparative analysis must be treated with caution. Specifically, the findings cannot be used to infer that non-medical induction of labour causes any of the adverse outcomes described.
1. Dahlen HG, Thornton C, Downe S, et al. Intrapartum interventions and outcomes for women and children following induction of labour at term in uncomplicated pregnancies: a 16-year population-based linked data study. BMJ Open. 2021;11(6):e047040.
2. Caughey AB, Sundaram V, Kaimal AJ, et al. Systematic review: elective induction of labor versus expectant management of pregnancy. Ann Intern Med. 2009;151(4):252-263, W253-263.
3. Stock SJ, Ferguson E, Duffy A, Ford I, Chalmers J, Norman JE. Outcomes of elective induction of labour compared with expectant management: population based study. BMJ. 2012;344:e2838.
We thank Prof. Roberts for his interest in the PATCH-Trauma trial. The PATCH-Trauma trial is by no means a criticism of the CRASH-2 trial.(1) Rather, it aims to evaluate the findings in a different setting. It remains paramount to externally validate results of trials whenever possible, regardless of how strong the effects may seem from a single trial.(2)
We note some disagreement regarding the background material. However, these are largely subjective views and should not detract from the key objective of the manuscript that was to publish the protocol for improved interpretation of the study findings. For example, our definition of "high income countries" is different. Whether the CRASH-2 trial included 10% or 2% of its study population from high income countries does not change the fact that most participants were in low- and middle-income countries. Similarly, while the CRASH-2 investigators did publish a secondary analysis of their data, it could not address the mechanism of tranexamic acid’s potential effectiveness in critical bleeding.(3)
We were encouraged that there were no critical comments regarding the methodology of the PATCH-Trauma trial or planned analysis. The PATCH-Trauma Trial has recruited 98.9% of its planned enrolment to date and we look forward to sharing the results of the study soon.
References
1. Shakur H, Roberts I, Bautista R, et al. Effects of tranexamic acid on death, vascular occlusive events, and blood tr...
We thank Prof. Roberts for his interest in the PATCH-Trauma trial. The PATCH-Trauma trial is by no means a criticism of the CRASH-2 trial.(1) Rather, it aims to evaluate the findings in a different setting. It remains paramount to externally validate results of trials whenever possible, regardless of how strong the effects may seem from a single trial.(2)
We note some disagreement regarding the background material. However, these are largely subjective views and should not detract from the key objective of the manuscript that was to publish the protocol for improved interpretation of the study findings. For example, our definition of "high income countries" is different. Whether the CRASH-2 trial included 10% or 2% of its study population from high income countries does not change the fact that most participants were in low- and middle-income countries. Similarly, while the CRASH-2 investigators did publish a secondary analysis of their data, it could not address the mechanism of tranexamic acid’s potential effectiveness in critical bleeding.(3)
We were encouraged that there were no critical comments regarding the methodology of the PATCH-Trauma trial or planned analysis. The PATCH-Trauma Trial has recruited 98.9% of its planned enrolment to date and we look forward to sharing the results of the study soon.
References
1. Shakur H, Roberts I, Bautista R, et al. Effects of tranexamic acid on death, vascular occlusive events, and blood transfusion in trauma patients with significant haemorrhage (CRASH-2): a randomised, placebo-controlled trial. Lancet 2010;376:23-32.
2. Rothwell PM. External validity of randomised controlled trials: “To whom do the results of this trial apply?”. The Lancet 2005;365:82-93.
3. Roberts I, Shakur H, Afolabi A, et al. The importance of early treatment with tranexamic acid in bleeding trauma patients: an exploratory analysis of the CRASH-2 randomised controlled trial. Lancet 2011;377:1096-101, 101.e1-2.
The BACPR would like to thank the ICCPR for their recent letter highlighting the work undertaken by both organisations. We are reassured to learn that the results of the ICCPR survey are similar to our own [1]. Both studies, conducted to support cardiovascular prevention and rehabilitation programmes, found that half of all cardiac rehabilitation services were cancelled during the first wave of COVID-19 (~March to June 2020). This is concerning because the closure of so many cardiac rehabilitation programmes is likely to have had a significant negative effect on patient outcomes, cause avoidable hospital admissions, and undermine government efforts to reduce the pressure on acute hospital and healthcare services, during the COVID-19 pandemic. We agree with the ICCPR that further work is needed to investigate whether cardiac rehabilitation services have been restored. The BACPR remain committed to undertaking research that guides decision making and would be happy to explore opportunities with the ICCPR to combine existing research datasets and conduct future collaborative projects.
We believe that it is essential that government, governing bodies, and local policy makers, support cardiac rehabilitation teams to resume the delivery of effective services. Whilst restrictions on face-to-face human contact remain in place, services should be supported to adopt and refine remotely delivered models of cardiac rehabilitation. As we demonstrate in our survey [1], significan...
The BACPR would like to thank the ICCPR for their recent letter highlighting the work undertaken by both organisations. We are reassured to learn that the results of the ICCPR survey are similar to our own [1]. Both studies, conducted to support cardiovascular prevention and rehabilitation programmes, found that half of all cardiac rehabilitation services were cancelled during the first wave of COVID-19 (~March to June 2020). This is concerning because the closure of so many cardiac rehabilitation programmes is likely to have had a significant negative effect on patient outcomes, cause avoidable hospital admissions, and undermine government efforts to reduce the pressure on acute hospital and healthcare services, during the COVID-19 pandemic. We agree with the ICCPR that further work is needed to investigate whether cardiac rehabilitation services have been restored. The BACPR remain committed to undertaking research that guides decision making and would be happy to explore opportunities with the ICCPR to combine existing research datasets and conduct future collaborative projects.
We believe that it is essential that government, governing bodies, and local policy makers, support cardiac rehabilitation teams to resume the delivery of effective services. Whilst restrictions on face-to-face human contact remain in place, services should be supported to adopt and refine remotely delivered models of cardiac rehabilitation. As we demonstrate in our survey [1], significant progress has been made in this regard and the BACPR are hopeful that the COVID-19 pandemic will catalyse a change in the way cardiac rehabilitation is delivered around the world, in the longer-term. Improving access to high quality home-based cardiac rehabilitation could enable more people to participate in this vital part of their cardiac recovery. As discussed in our survey [1], a concerted effort should be made to eliminate the barriers relating to remotely delivered cardiac rehabilitation. The BACPR will be working hard to ensure that this vital message is not lost as countries around the world eventually begin to recover from the effects of COVID-19.
1. O'Doherty, A., F., et al., How has technology been used to deliver cardiac rehabilitation during the COVID-19 pandemic? An international cross-sectional survey of healthcare professionals conducted by the BACPR. BMJ Open, 2021. 11:e046051.
Since the publication of the article, it has come to the authors’ attention that the flowchart (Figure 1) can be misleading. According to the flow chart, 1 738 358 pregnancies ending as an abortion were excluded due to missing gestational age or gestational age >140 days. This seems to be a large proportion of missing data, which could question the validity of the coding of abortions in the patient registry. It was, however, not at missing data problem but was due to technical reasons. In the raw data, a unique abortion could be recorded more than once. Removing duplicates is therefore a regular part of the data cleaning process when working with these data. In our data, 1 733 799 abortions were removed because they were duplicates, which would have been the correct designation in the flow chart rather than missing gestational age. Of notice, the final number of pregnancies included in the analyses was correct.
Anne Staub Rasmussen
Christian Fynbo Christiansen,
Niels Uldbjerg,
Mette Nørgaard
Thank you for your research regarding this retrospective population linked data in NSW.
We wish to make a number of comments regarding the methods and conclusions reached.
Firstly, the premise of retrospectively comparing birth outcomes for induction versus spontaneous labour at a particular gestation is an erroneous one. It is not possible to elect to go into spontaneous labour. The only option available to women is elect to have an induction at a certain gestation, or to continue with the pregnancy, i.e. expectant management. Expectant management may include the pregnancy going post-dates, requiring an IOL at a later gestation, or the development of complications that are known to increase beyond 40 weeks including preeclampsia, placental insufficiency, stillbirth and macrosomia.
It is for this simple reason that prospective RCT data that compares IOL at 39-40 weeks versus expectant management demonstrate a clear reduction in the rate of caesarean section, third and fourth degree perineal tears, and a reduction in perinatal adverse outcomes.
It is not possible with your data to make any comment regarding the outcomes of IOL for no medical reason versus expectant management. Given, in reality, this is the only choice that women are able to make, we do not believe that your conclusion, that women may have an increased rate of caesarean section and adverse outcomes if they elect for an IOL, is supported at all...
Thank you for your research regarding this retrospective population linked data in NSW.
We wish to make a number of comments regarding the methods and conclusions reached.
Firstly, the premise of retrospectively comparing birth outcomes for induction versus spontaneous labour at a particular gestation is an erroneous one. It is not possible to elect to go into spontaneous labour. The only option available to women is elect to have an induction at a certain gestation, or to continue with the pregnancy, i.e. expectant management. Expectant management may include the pregnancy going post-dates, requiring an IOL at a later gestation, or the development of complications that are known to increase beyond 40 weeks including preeclampsia, placental insufficiency, stillbirth and macrosomia.
It is for this simple reason that prospective RCT data that compares IOL at 39-40 weeks versus expectant management demonstrate a clear reduction in the rate of caesarean section, third and fourth degree perineal tears, and a reduction in perinatal adverse outcomes.
It is not possible with your data to make any comment regarding the outcomes of IOL for no medical reason versus expectant management. Given, in reality, this is the only choice that women are able to make, we do not believe that your conclusion, that women may have an increased rate of caesarean section and adverse outcomes if they elect for an IOL, is supported at all by your data.
As you note, RCT meta-analyses evidence shows the opposite to occur. Whilst exact calculations are not possible from your data, it would appear that IOL at 39-40 weeks compared to expectant management (which may result in either spontaneous labour at a later gestation or IOL at a later gestation with higher risk of adverse outcomes) likely result in similar findings in your study to those demonstrated in the RCTs.
Secondly, we question the study population. As you note, the records were not able to be verified for accuracy, and it is noted that such records are often incomplete. We believe it is likely that a significant proportion of those included as ‘no medical indication for IOL’ did in fact have a medical indication.
In our knowledge of private and public obstetrics in Australia over the timeframe studied (which is prior to the ARRIVE trial and prior to the publication of the meta analyses showing benefit and safety of IOL for low risk women), we would be very surprised if 1 in every 6 inductions were being performed for no medical reason. Even in 2021, with evidence of both safety and benefit, IOL is not offered without a medical reason, and as such it is exceedingly rare for an induction to be performed in our busy maternity centre for no medical indication.
The finding that women who were induced differed significantly on all maternal and child characteristics is further reason to doubt the accuracy of the study population. The two groups (IOL versus spontaneous labour) that you have compared were two clearly disparate groups that differed statistically significantly on all characteristics.
Thirdly, we would like to draw particular attention to the exclusion of all women who suffered a stillbirth from your data. Reducing the tragedy of stillbirth is a national health priority. RCT evidence consistently demonstrates a significant reduction in stillbirth for IOL compared to expectant management. You state that ‘our data accords with other whole population, longer term observational studies, such as that reported recently from Denmark’. We disagree. Crucially, the Denmark trial, which was a well designed prospective trial comparing IOL at 41 weeks compared to IOL at 42 weeks, was stopped early due to a significantly higher rate of perinatal mortality in the expectant group. Five stillbirths occured in the expectant group compared to none in the induction group. We believe the inability to assess stillbirth risk, and the omission of stillbirth from your data, further limits the interpretation and validity of any findings. This is particularly the case given reduction of post-term stillbirth is one of the primary reasons women may choose to request an induction of labour.
Lastly, despite the RCT evidence of safety and the clear reduction in caesarean rate, we wish to make it clear that we are not advocating for IOL of all low risk women between 39 and 40 weeks.
We wholeheartedly support the many women who have a low risk pregnancy and place high value on having a birth experience that is free from medical intervention. We strongly support this woman and her choice. Another woman, given the same information, may elect to request an IOL at 39-40 weeks to reduce their risk of caesarean section, third and fourth degree tears, and post-term stillbirth. Equally, we support this woman and her choice.
We believe that our role as pregnancy care providers is to provide clear and current evidence of the risks and benefits of IOL and to support women in their birth choices. We believe that this retrospective study, that does not have the ability to compare IOL with expectant management, and excludes stillbirth as an outcome, does not alter the high level evidence from the multiple prospective RCT findings on this important topic in pregnancy care.
Atmore et al (2021) have reported findings from a general practice patient records review in New Zealand.1 Main research question was to compare harms between rural and urban locations. Sampling design was a stratified sampling design with unequal probabilities of selection from strata.2 Authors reported “weights developed from the SHARP study data were applied to enable generalisability of results to the NZ population”. Analyses include Chisquare test, Fishers exact test, independent sample t-test, Mann-Whitney test, Wald test, Poisson regression, and ordinal logistic regression. Some of these procedures cannot accommodate any type of weights, some can accommodate frequency weights but not sampling weights. So, with these procedures authors either may not have used sampling weights or may have incorrectly used them as frequency weights. Closer look at the presented results shows most, if not all, percentages reported are simply the simple percentages observed in data, ignoring sampling weights. In stratified sampling designs, researchers can observe any desired strata-specific percentage by altering the strata-specific sampling fraction of participants, therefore not using sampling weights or incorrectly using them to compare outcomes between strata almost always invalidate results. Further, authors have interpreted main effects from the regression models ignoring interaction effects. For these reasons, the results presented in the Atmore et al paper are unreliable, and t...
Atmore et al (2021) have reported findings from a general practice patient records review in New Zealand.1 Main research question was to compare harms between rural and urban locations. Sampling design was a stratified sampling design with unequal probabilities of selection from strata.2 Authors reported “weights developed from the SHARP study data were applied to enable generalisability of results to the NZ population”. Analyses include Chisquare test, Fishers exact test, independent sample t-test, Mann-Whitney test, Wald test, Poisson regression, and ordinal logistic regression. Some of these procedures cannot accommodate any type of weights, some can accommodate frequency weights but not sampling weights. So, with these procedures authors either may not have used sampling weights or may have incorrectly used them as frequency weights. Closer look at the presented results shows most, if not all, percentages reported are simply the simple percentages observed in data, ignoring sampling weights. In stratified sampling designs, researchers can observe any desired strata-specific percentage by altering the strata-specific sampling fraction of participants, therefore not using sampling weights or incorrectly using them to compare outcomes between strata almost always invalidate results. Further, authors have interpreted main effects from the regression models ignoring interaction effects. For these reasons, the results presented in the Atmore et al paper are unreliable, and therefore the conclusions arrived from those results are not trustworthy.
References:
(1) Atmore C, Dovey S, Gauld R, et al. Do people living in rural and urban locations experience differences in harm when admitted to hospital? A cross-sectional New Zealand general practice records review study. BMJ Open 2021;11:e046207. doi:10.1136/bmjopen-2020-046207
(2) Dovey SM, Leitch S, Wallis KA, et al. Epidemiology of patient harms in New Zealand: protocol of a general practice records review study. JMIR Res Protoc 2017;6:e10.
The study authors acknowledge the delay from the point of submission of the article to final publication. This delay inevitably means that we were unable to offer a more current version but acknowledge that the field may have moved on as stated in implications of practice. We note that the value of systematic reviews is maximised when they are up-to-date and agree with the author that there may be new relevant evidence which has been published.
We would like to thank the author for highlighting the issue of a much greater magnitude than the specific one related to our systematic review. Over the past two decades, several authors and organisations highlighted the tension between the average length of time for conducting a systematic review and long editorial process needed to publish the systematic review in a journal (median time: 15 months) versus the need for updating systematic reviews that arises due to emergence of new relevant evidence published over time (median time: 1-5 years).(1-5)
We believe that the COVID-19 pandemic contributed towards even more prolonged duration of editorial process than usual by overburdening its staff with multiple submissions of studies on SARS-CoV-2 infection. Moreover, the topic of SARS-CoV-2 infection is a new and rapidly emerging field where the evidence for any given research question is still evolving, thus being insufficient and uncertain. In the context of the COVID-19 pandemic and the fast pace of published literat...
The study authors acknowledge the delay from the point of submission of the article to final publication. This delay inevitably means that we were unable to offer a more current version but acknowledge that the field may have moved on as stated in implications of practice. We note that the value of systematic reviews is maximised when they are up-to-date and agree with the author that there may be new relevant evidence which has been published.
We would like to thank the author for highlighting the issue of a much greater magnitude than the specific one related to our systematic review. Over the past two decades, several authors and organisations highlighted the tension between the average length of time for conducting a systematic review and long editorial process needed to publish the systematic review in a journal (median time: 15 months) versus the need for updating systematic reviews that arises due to emergence of new relevant evidence published over time (median time: 1-5 years).(1-5)
We believe that the COVID-19 pandemic contributed towards even more prolonged duration of editorial process than usual by overburdening its staff with multiple submissions of studies on SARS-CoV-2 infection. Moreover, the topic of SARS-CoV-2 infection is a new and rapidly emerging field where the evidence for any given research question is still evolving, thus being insufficient and uncertain. In the context of the COVID-19 pandemic and the fast pace of published literature related to SARS-CoV-2 infection, any systematic review on this topic is at high risk of becoming out-of-date even in a short time period after the review is completed. It would be logistically impossible to keep abreast of all these developments and keep updating all systematic reviews continuously, especially after their publication. Even the organisation such as Cochrane, which invested substantial efforts in keeping systematic reviews up-to-date with the goal of updating their systematic reviews every two years, find it difficult to maintain high update rates.(4) Today’s technological advances have made it possible to develop and evaluate new publication formats that could facilitate the updating process. Cochrane introduced the concept of ‘living systematic reviews’ which are online evidence summaries, continuously updated as new relevant evidence becomes available. This approach overcomes the limitations of the traditional publication ‘static’ format and advocates creation of a single easily edited and evolving document for a systematic review including its registration, protocol stage, and change of results as/if they become available.(6)
To follow-up the concerns that the author raised about our review, we respectfully disagree that our review is of doubtful relevance when, in fact the two newly published systemic reviews(7-8) cited by the author lack credibility in terms of the methods used and reporting standards. The methodological quality of our review is high, searches inclusive and importantly methods and results are transparent for readers, which speaks for its replicability. Our systematic review was already in the peer review process (since August 2020) when both of the new systematic reviews were published in 2021.(7-8) We note however, that the quality of reporting of Petrelli et al (2021)(7) is questionable, at best a brief correspondence, and that therefore, the validity of the findings are uncertain. The other two citations provided by the author are commentary pieces.
The second systematic review cited, Liu et al 2021,(8) commenced after our systematic review began (PROSPERO registration 29/10/2020). Although the reporting of this review is improved when compared to Petrelli et al (2021) the design of included studies and the rigour of methodology of synthesis is doubtful. The authors do not present a transparent description of full study methods and analysis (i.e., example search strategy, results from the quality appraisal, studies excluded with reasons provided). Liu et al (2021) was limited to studies of association between vitamin D levels and the COVID-19 outcome and excluded studies that evaluated effects of supplemental vitamin D on the COVID-19 based outcome.
Readers of this review will note from their report that the authors included 10 case-control studies including 376,596 participants. One study by Hastie and colleagues contributed 348,598 of those, was included in our review and did not support a potential link between 25(OH)D concentrations and the risk of severe COVID-19 infection. The inclusion of only case-control studies does not allow to determine the temporal relationship between the vitamin D levels or supplementation and the development COVID-19 related outcome. Case-control studies are prone to confounding and selection bias. This review does not clarify if or how these issues were dealt in individual studies. Nor does this review describe how the risk of bias of these studies was assessed.
The meta-analysis revealed a high degree of heterogeneity that suggests inadequacy of the pooled estimate. The meta-analysis of the 4 case-control studies had high heterogeneity for COVID-19 infection (I2 = 64.9%, p = 0.036) and the eight studies included to examine Vitamin D levels in COVID-19-positive and-negative participants was even larger (I2 = 89.6%). Highly significant heterogeneity adds to the uncertainty of findings that should be interpreted with caution. Unfortunately, the source of heterogeneity was not explored (e.g., the definition of exposure [vitamin D level] was inconsistent across studies) and authors only used a random effects model to address this significant heterogeneity. Subsequently Liu et al (2021), highlight in their review that: “Formal proof for an effect remains to be determined by randomized controlled trials.” We support this conclusion in our review.
To limit research waste whilst providing evidence to answer the question of whether vitamin D supplementation or level associated with susceptibility to severe betacoronavirus infection (SARS-CoV, MERS-CoV, SARS-CoV-2), clinical course, morbidity and mortality outcomes, we suggest that an update to our review should be conducted once the clinical trials listed in our study have reported results. To facilitate future updates we provided our search strategy in our additional file. To supplement this, we point readers to the Cochrane living systematic of RCTs that assessed the safety and efficacy of vitamin D supplementation for the treatment of COVID-19 in comparison to an active comparator, placebo, or standard of care alone.(9) This review identified three RCTs with 356 participants, of whom 183 received vitamin D. The control groups consisted of placebo treatment or standard of care alone. The authors found that evidence was insufficient to conclude if vitamin D supplementation was effective in reducing all cause mortality and improving quality of life. This is in line with the findings of our systematic review.
Finally, we call for researchers to thoroughly search PROSPERO for registered reviews/updates before commencing multiple reviews on the same topic in parallel. Details on the completed/ongoing clinical trials which were citied in our review are provided below which may be helpful to readers:
COvid-19 and Vitamin D Supplementation: a Multicenter Randomized Controlled Trial of High Dose Versus Standard Dose Vitamin D3 in High-risk COVID-19 Patients (CoVitTrial). NCT04344041 – completed (no published results), 260 participants, See published protocol.(10)
The VITDALIZE Study: Effect of High-dose Vitamin D3 on 28-day Mortality in Adult Critically Ill Patients (VITDALIZE). NCT03188796 - Recruiting. Completion date February 2023, 2400 participants. See published protocol.(11)
Note that NCT04351490 has been withdrawn due to changes in study design and funding.
References
1 Sampson M, Shojania KG, Garritty C, Horsley T, Ocampo M, Moher D. Systematic reviews can be produced and published faster. Journal of clinical epidemiology. 2008;61(6):531-6. doi:10.1016/j.jclinepi.2008.02.004
2 Tsertsvadze A, Chen YF, Moher D, Sutcliffe P, McCarthy N. How to conduct systematic reviews more expeditiously? Systematic reviews. 2015;4(1):160. doi:10.1186/s13643-015-0147-7.
3 Shojania KG, Sampson M, Ansari MT, Ji J, Doucette S, Moher D. How quickly do systematic reviews go out of date? A survival analysis. Annals of internal medicine. 2007;147(4):224-33.
4 Jaidee W, Moher D, Laopaiboon M. Time to update and quantitative changes in the results of cochrane pregnancy and childbirth reviews. PLoS ONE [Electronic Resource]. 2010;5(7):e11553.
5 Peterson K, McDonagh MS, Fu R. Decisions to update comparative drug effectiveness reviews vary based on type of new evidence. Journal of clinical epidemiology. 2011;64(9):977-84.
6 Elliott JH, Turner T, Clavisi O, Thomas J, Higgins JP, Mavergames C et al. Living systematic reviews: an emerging opportunity to narrow the evidence-practice gap. PLoS medicine. 2014;11(2):e1001603. doi:10.1371/journal.pmed.1001603.
7 Petrelli F, Luciani A, Perego G, Dognini G, Colombelli PL, Ghidini A. Therapeutic and prognostic role of vitamin D for COVID-19 infection: A systematic review and meta-analysis of 43 observational studies. J Steroid Biochem Mol Biol. 2021 Mar 26;211:105883. doi: 10.1016/j.jsbmb.2021.105883. Epub ahead of print. PMID: 33775818; PMCID: PMC7997262.
8 Liu N, Sun J, Wang X, Zhang T, Zhao M, Li H. Low vitamin D status is associated with coronavirus disease 2019 outcomes: a systematic review and meta-analysis. Int J Infect Dis. 2021 Mar;104:58-64. doi: 10.1016/j.ijid.2020.12.077. Epub 2021 Jan 2. PMID: 33401034; PMCID: PMC7833186.
9 Stroehlein JK, Wallqvist J, Iannizzi C, Mikolajewska A, Metzendorf M-I, Benstoem C, Meybohm P, Becker M, Skoetz N, Stegemann M, Piechotta V. Vitamin D supplementation for the treatment of COVID-19: a living systematic review. Cochrane Database of Systematic Reviews 2021, Issue 5. Art. No.: CD015043.DOI: 10.1002/14651858.CD015043.
10 Annweiler C, Beaudenon M, Gautier J, Simon R, Dubée V, Gonsard J, Parot-Schinkel E; COVIT-TRIAL study group. COvid-19 and high-dose VITamin D supplementation TRIAL in high-risk older patients (COVIT-TRIAL): study protocol for a randomized controlled trial. Trials. 2020 Dec 28;21(1):1031. doi: 10.1186/s13063-020-04928-5.
11 Amrein K, Parekh D, Westphal S, Preiser JC, Berghold A, Riedl R, Eller P, Schellongowski P, Thickett D, Meybohm P; VITDALIZE Collaboration Group. Effect of high-dose vitamin D3 on 28-day mortality in adult critically ill patients with severe vitamin D deficiency: a study protocol of a multicentre, placebo-controlled double-blind phase III RCT (the VITDALIZE study). BMJ Open. 2019 Nov 12;9(11):e031083. doi: 10.1136/bmjopen-2019-031083.
We appreciate the interest that Dr. Pedersen has shown in our paper, but he has apparently misunderstood some aspects of our analysis. In the analysis of the stillbirth data, we first described the dependence of log (rate) on calendar year by a straight line. Next, we allowed the slope to change from 2011 onwards (a so-called linear spline with a knot at 2011). This did not improve the fit significantly. This is the analysis reported in our paper. Besides we also tried to see if a change in intercept from 2011 onwards would lead to a significantly better fit. This was not the case. This latter model is the one that Dr. Pedersen considers, but this was not the one presented in our paper.
We are also concerned about Dr. Pedersen’s suggestion that we have been unresponsive to his questions. We can document at least 11 email correspondences and two face to face meetings with Dr. Pedersen to accommodate Dr. Pedersen’s wish for more information and discussion of our analyses. These mails and meetings have also included the Lead Professor of Dr. Pedersen’s department and a Professor in Biostatistics from Aarhus University. The Professor in Biostatistics has confirmed to all included in the meetings and in the additional emails that our analysis as well as our conclusions in the paper were valid.
Eva Rydahl, Eugene Declercq, Mette Juhl, Rikke Damkjær Maimburg
De Rubeis et al. conducted a systematic review to evaluate the effect of disasters, including pandemics, on cardiometabolic outcomes (1). Clinical outcomes were checked ≥1 month following the disaster. The effects of exposure to disaster during pregnancy/childhood and during adulthood were included, and increased cardiovascular disease incidence or mortality, diabetes and obesity were observed in each study. Although the biological mechanisms of the association might be complex, long-term effects of disasters on cardiometabolic health should be explored to elucidate prevention strategies against forthcoming disasters (2-4).
References
1. e Rubeis V, Lee J, Anwer MS, et al. Impact of disasters, including pandemics, on cardiometabolic outcomes across the life-course: a systematic review. BMJ Open. 2021;11(5):e047152.
2. Chua MWJ. Managing patients with obesity in the post COVID-19 world: Time to sharpen the saw. Obes Res Clin Pract. 2021;15:85-88.
3. Narita K, Hoshide S, Tsoi K, et al. Disaster hypertension and cardiovascular events in disaster and COVID-19 pandemic. J Clin Hypertens (Greenwich). 2021 ;23(3):575-583.
4. Burg MM, Soufer R. Post-traumatic Stress Disorder and Cardiovascular Disease. Curr Cardiol Rep. 2016;18(10):94
Dear Dr. Walid Al-Wali et al,
Show MoreThank you for interest in our work, particularly for your comments on the published protocol titled: Estimating the vaccine confidence levels among healthcare students and staff of a tertiary institution in South Africa.
As you rightly observed, and as stated in the article, the study population is healthcare students and staff of a tertiary institution in South Africa. In this particular setting (a medical campus) a significant number of medical students in their senior years as well as staff have direct dealings with, and exposure to patients in the adjacent teaching hospital as part of their studies and routine duties. These, therefore, were considered as part of the frontline healthcare workers that were prioritized for the receipt of the COVID 19 vaccines, the roll-out of which at the time of the design of our study, was imminent. One of the main aims of our study was to investigate the intention to receive a COVID 19 vaccine when one becomes available. This cogent reason makes the population described above ideal for our study.
Moreover, the selected study population is relevant to gaining some insight on the probable vaccine sentiments of future healthcare workers, identifying any issues of concern and planning how to mitigate them, and gauging how well they might likely advocate for vaccine acceptance. The representability of the current population views (though they are part of the larger population and possibly part...
I would like to congratulate Hannah Dahlen and colleagues on their recent publication in BMJ Open (1), particularly with respect to their follow-up of longer-term outcomes for infants born following induction of labour between 37 and 41 completed weeks gestational age compared with women who had a spontaneous onset of labour.
Show MoreDahlen et al found that adverse maternal outcomes including caesarean section, instrumental birth, epidural use (potentially indicating a more painful and/or longer labour), episiotomy and post-partum haemorrhage were more common among women with an induced labour compared with women who went into spontaneous labour.
They list absence of an intention-to-treat analysis as a weakness in the study design, but go on to say, “the data sources have a good track record of accuracy, so we do not believe these errors are likely to be large, or that they would have significantly influenced the direction of effect of the outcomes.”
However, even if the data were perfectly accurate, the lack of intention-to-treat analysis causes a selection bias to an extent which makes it impossible to assess the impact of non-medically indicated induction of labour on maternal, neonatal, and child outcomes.
In a randomised trial of planned induction of labour at a given gestational age, an intention-to-treat analysis will include all randomised women, including those who went on to have a later medically indicated induction of labour. Similarly, in an o...
We thank Prof. Roberts for his interest in the PATCH-Trauma trial. The PATCH-Trauma trial is by no means a criticism of the CRASH-2 trial.(1) Rather, it aims to evaluate the findings in a different setting. It remains paramount to externally validate results of trials whenever possible, regardless of how strong the effects may seem from a single trial.(2)
We note some disagreement regarding the background material. However, these are largely subjective views and should not detract from the key objective of the manuscript that was to publish the protocol for improved interpretation of the study findings. For example, our definition of "high income countries" is different. Whether the CRASH-2 trial included 10% or 2% of its study population from high income countries does not change the fact that most participants were in low- and middle-income countries. Similarly, while the CRASH-2 investigators did publish a secondary analysis of their data, it could not address the mechanism of tranexamic acid’s potential effectiveness in critical bleeding.(3)
We were encouraged that there were no critical comments regarding the methodology of the PATCH-Trauma trial or planned analysis. The PATCH-Trauma Trial has recruited 98.9% of its planned enrolment to date and we look forward to sharing the results of the study soon.
References
Show More1. Shakur H, Roberts I, Bautista R, et al. Effects of tranexamic acid on death, vascular occlusive events, and blood tr...
The BACPR would like to thank the ICCPR for their recent letter highlighting the work undertaken by both organisations. We are reassured to learn that the results of the ICCPR survey are similar to our own [1]. Both studies, conducted to support cardiovascular prevention and rehabilitation programmes, found that half of all cardiac rehabilitation services were cancelled during the first wave of COVID-19 (~March to June 2020). This is concerning because the closure of so many cardiac rehabilitation programmes is likely to have had a significant negative effect on patient outcomes, cause avoidable hospital admissions, and undermine government efforts to reduce the pressure on acute hospital and healthcare services, during the COVID-19 pandemic. We agree with the ICCPR that further work is needed to investigate whether cardiac rehabilitation services have been restored. The BACPR remain committed to undertaking research that guides decision making and would be happy to explore opportunities with the ICCPR to combine existing research datasets and conduct future collaborative projects.
We believe that it is essential that government, governing bodies, and local policy makers, support cardiac rehabilitation teams to resume the delivery of effective services. Whilst restrictions on face-to-face human contact remain in place, services should be supported to adopt and refine remotely delivered models of cardiac rehabilitation. As we demonstrate in our survey [1], significan...
Show MoreSince the publication of the article, it has come to the authors’ attention that the flowchart (Figure 1) can be misleading. According to the flow chart, 1 738 358 pregnancies ending as an abortion were excluded due to missing gestational age or gestational age >140 days. This seems to be a large proportion of missing data, which could question the validity of the coding of abortions in the patient registry. It was, however, not at missing data problem but was due to technical reasons. In the raw data, a unique abortion could be recorded more than once. Removing duplicates is therefore a regular part of the data cleaning process when working with these data. In our data, 1 733 799 abortions were removed because they were duplicates, which would have been the correct designation in the flow chart rather than missing gestational age. Of notice, the final number of pregnancies included in the analyses was correct.
Anne Staub Rasmussen
Christian Fynbo Christiansen,
Niels Uldbjerg,
Mette Nørgaard
Dear Professor Dahlen et al
Thank you for your research regarding this retrospective population linked data in NSW.
We wish to make a number of comments regarding the methods and conclusions reached.
Firstly, the premise of retrospectively comparing birth outcomes for induction versus spontaneous labour at a particular gestation is an erroneous one. It is not possible to elect to go into spontaneous labour. The only option available to women is elect to have an induction at a certain gestation, or to continue with the pregnancy, i.e. expectant management. Expectant management may include the pregnancy going post-dates, requiring an IOL at a later gestation, or the development of complications that are known to increase beyond 40 weeks including preeclampsia, placental insufficiency, stillbirth and macrosomia.
It is for this simple reason that prospective RCT data that compares IOL at 39-40 weeks versus expectant management demonstrate a clear reduction in the rate of caesarean section, third and fourth degree perineal tears, and a reduction in perinatal adverse outcomes.
It is not possible with your data to make any comment regarding the outcomes of IOL for no medical reason versus expectant management. Given, in reality, this is the only choice that women are able to make, we do not believe that your conclusion, that women may have an increased rate of caesarean section and adverse outcomes if they elect for an IOL, is supported at all...
Show MoreAtmore et al (2021) have reported findings from a general practice patient records review in New Zealand.1 Main research question was to compare harms between rural and urban locations. Sampling design was a stratified sampling design with unequal probabilities of selection from strata.2 Authors reported “weights developed from the SHARP study data were applied to enable generalisability of results to the NZ population”. Analyses include Chisquare test, Fishers exact test, independent sample t-test, Mann-Whitney test, Wald test, Poisson regression, and ordinal logistic regression. Some of these procedures cannot accommodate any type of weights, some can accommodate frequency weights but not sampling weights. So, with these procedures authors either may not have used sampling weights or may have incorrectly used them as frequency weights. Closer look at the presented results shows most, if not all, percentages reported are simply the simple percentages observed in data, ignoring sampling weights. In stratified sampling designs, researchers can observe any desired strata-specific percentage by altering the strata-specific sampling fraction of participants, therefore not using sampling weights or incorrectly using them to compare outcomes between strata almost always invalidate results. Further, authors have interpreted main effects from the regression models ignoring interaction effects. For these reasons, the results presented in the Atmore et al paper are unreliable, and t...
Show MoreThe study authors acknowledge the delay from the point of submission of the article to final publication. This delay inevitably means that we were unable to offer a more current version but acknowledge that the field may have moved on as stated in implications of practice. We note that the value of systematic reviews is maximised when they are up-to-date and agree with the author that there may be new relevant evidence which has been published.
We would like to thank the author for highlighting the issue of a much greater magnitude than the specific one related to our systematic review. Over the past two decades, several authors and organisations highlighted the tension between the average length of time for conducting a systematic review and long editorial process needed to publish the systematic review in a journal (median time: 15 months) versus the need for updating systematic reviews that arises due to emergence of new relevant evidence published over time (median time: 1-5 years).(1-5)
We believe that the COVID-19 pandemic contributed towards even more prolonged duration of editorial process than usual by overburdening its staff with multiple submissions of studies on SARS-CoV-2 infection. Moreover, the topic of SARS-CoV-2 infection is a new and rapidly emerging field where the evidence for any given research question is still evolving, thus being insufficient and uncertain. In the context of the COVID-19 pandemic and the fast pace of published literat...
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