We would like to thank the previous respondent (27.01.23) for their careful reading of our paper and for sharing their thoughts. Having considered it, the response assumes that our study included a manipulation check which was based on the emotion variable. However, this was not the case. We are not trying to manipulate how uncertain the participants actually feel – we expect them to feel uncertain after receiving conflicting information regardless of whether or not uncertainty is expressed in the vaccine announcement. The point of the paper is that when governments fail to express the uncertainty that people end up encountering, this reduces trust in them. How uncertain participants feel is therefore not a manipulation check as it is not conceptually linked to our manipulation, i.e. uncertainty expressed by the government. If we had wanted to include a manipulation check, it would have been about the perception that the government official is certain about the effectiveness of the vaccine.

Having said that, the question of experienced uncertainty is still an interesting research question. Although there was some evidence that the manipulation did affect the dynamics of uncertainty (i.e., there was a significantly larger increase in uncertainty in the “certain” than in the “uncertain” condition; F(1,326)=9.27, p=0.003)), this is not required for our conceptual model. Even if we were to use the uncertain emotion variable as a manipulation check, it would not be appropriate to use it as an independent variable in a mediator model in a setting where it is influenced by numerous exogenous factors. We do not expect that an experimental manipulation of this nature would have a large effect on a variable like vaccine uncertainty, that has so many social determinants outside of the experimental setting. It makes sense that those who feel more uncertain about getting the vaccine are going to have lower intentions to get it, which is precisely why some public health communicators avoid expressing uncertainty. Our point here is that when communicators express uncertainty, rather than exacerbating the public’s uncertainty, this helps to protect them against a loss of trust if problems surface later and maintains vaccine intentions in the longer term.

Although we do not agree that the uncertainty emotion data are problematic for the interpretation of the paper, we thank the respondent for raising this interesting question about how the manipulation affects experienced uncertainty.

Dear Editor,

To Prof Forrest and the authors of the Chaudhary et al paper(1): Thank you for your response to our review(2) in which you highlight that there was a significant reduction in alcohol-related liver disease (ALD) discharges following the introduction of minimum unit pricing (MUP) at your unit. This is an important point to highlight as a misrepresentation of the Chaudhary et al study in our review.

In our review, we reported the outcome measure of mean weekly ALD discharges before and after MUP for 'All hospital episodes' which did not reach pre-defined significance (6.2 versus 5.2; p = 0.123) in the Chaudhary et al study, however the outcomes for 'individual patients' and those 'actively drinking' did indeed reach pre-defined significance and should have been included in our review. These outcomes from the Chaudhary et al study would certainly be consistent with the overall conclusion of our review, adding further support to the impact of MUP reducing alcohol-related hospital burden as you have highlighted.

We would also like to correct the reference to your study in the main text of our review which should read “Chaudhary et al” and not “Ferguson et al” (found under ‘Results’, subheading ‘Natural experiments’).

References
1. Chaudhary S, MacKey W, Duncan K, Forrest EH. Changes in Hospital Discharges with Alcohol-Related Liver Disease in a Gastroenterology and General Medical Unit Following the Introduction of Minimum Unit Pricing of Alcohol: The GRI Q4 Study. Alcohol and Alcoholism 2022; 57(4): 477–482.
2. Maharaj T, Angus C, Fitzgerald N, et al. Impact of minimum unit pricing on alcohol-related hospital outcomes: systematic review. BMJ Open 2023; 13: e065220. doi: 10.1136/bmjopen-2022-065220

Dear Editor,
The article by Yang et al. (2022) is fundamentally flawed due to a number of serious methodological shortcomings. These deficits are of such crucial relevance that it is in our view highly doubtful whether the conclusions the authors draw from their research are valid.

1) Data extraction is not transparent and sometimes false:
We were not able to replicate any of the values included in the main analysis of pain (Figure 4). In at least one study, values were extracted from the wrong group. In two further studies, the given values are incompatible with the values reported in the study. In at least three studies, sample sizes were falsely extracted.
Specifically:
Only in one of the included studies (Bishop et al., 2016) the values given in Figure 4 (Mean, SD) were found (Table 6, Bishop et al., 2016). However, the values of the control group were extracted from the false group (see below). For all other included studies, the values (Mean, SD) given in Figure 4 were not found. We were not able to find a description of how the authors may have transformed the values to explain the disagreement. In some studies, the given values in Figure 4 are not only not replicable but are incompatible with the values reported in the studies:
o In Bishop et al. (2016), values were extracted from the false group. Values were taken from standard care group but Yang et al. stated in Table 1 to have used the placebo acupuncture group as control group. The placebo acupuncture group actually had better pain scores than the experimental group. This is the opposite effect of what is used in Figure 4.
o Elden et al. (2005) reported morning and evening pain values post treatment in three groups. For all three groups and both measures (morning, evening), Elden et al. (2005) reported different medians. However, in Figure 4, equal means are given for experimental and control group for Elden et al. (2008) (which is a follow-up publication of the same study as Elden et al., 2005; see below).
o Lund et al. (2006) compared deep and superficial acupuncture. They did not report mean values but concluded that, regarding pain levels, "according to our study, there is not enough evidence of different treatment effects between the two stimulation modes of acupuncture". However, in Figure 4, the effect estimate presented for Lund et al. (2006) strongly favors the experimental group und the confidence interval does not include 0.
o In at least three studies, the extracted sample sizes were too large. Here, Yang et al. seemed to have used the number of participants that were included in the beginning of the study but failed to recognize that the analysis was done for a smaller number of patients. In the following, actual and falsely reported numbers are given for the groups Yang et al. presented in Table 1 (experimental group / control group): Bishop et al. (2016) reported 32 / 27, Yang et al. used 42 / 41; Ekdahl and Petersson (2010) reported 16 / 16, Yang et al. used 20 / 20; Elden et al. (2005) reported 107 / 108, Yang et al. used 130 / 125.

2) The same study is included twice:
Yang et al. included two publications of the same study (Elden et al., 2008; Elden et al., 2005) and presented them as two different studies in Table 1 and throughout the manuscript. Elden et al. (2005) reported pain endpoints whereas Elden et al. (2008) did not report values of pain. In contrast to that, in Figure 4, pain values are assigned to Elden et al. (2008).

3) The choices of the comparator group are not comprehensible:
Five of the nine included studies analyzed more than two groups (e.g. true acupuncture, placebo acupuncture, and standard care). Yang et al. did not give reasons for their choices of which group is used as control group. When three- or four-armed studies included both a placebo acupuncture group and a standard care group, Yang et al. sometimes chose the placebo acupuncture group as control (Bishop et al., 2016) and sometimes the standard care group (Jorge et al., 2019; Wang et al., 2009). One study (Ekdahl and Petersson, 2010) compared two acupuncture groups where the intervention was equal but began at different gestational weeks. It is not transparent why one of the groups was chosen as experimental group and the other one as control group.

3) Effects were pooled and interpreted as significant results with staggering heterogeneity and scarcity of data:
Despite the major heterogeneity observed, studies were pooled and effects were presented as statistically significant. This is contrary to the Cochrane recommendations for dealing with large heterogeneity (Cochrane Handbook Section 10.10.3 “Strategies for addressing heterogeneity” (https://training.cochrane.org/handbook/current/chapter-10#section-10-10-3): “1. Check again that the data are correct / 2. Do not do a meta-analysis”)

4) Choice between fixed-effect-model and random-effects-model was done in hindsight:
The authors stated “If p<0.1 or I**2 >50% we combined results using a random-effect model (29).” This is considered as bad practice, see, e.g. Borenstein et al. (2010) (https://doi.org/10.1002/jrsm.12): “In some circles, researchers tend to start with the fixed-effect model, and then switch to the random-effects model if there is a compelling reason to do so. Usually, this means that the test for heterogeneity across studies is statistically significant. This is a bad idea for many reasons.”
Furthermore, the cited reference (29) gives no justification for the applied approach.

In addition to the above points, some further issues came to our attention:
Figure 6 is falsely labelled. The left side of the forest plot should favor experimental.
The choice of the pain endpoint is not transparent: The included studies collected multiple different measures of VAS-pain. Two studies (Wedenberg et al., 2000; Elden et al., 2005) collected morning and evening values. One study (Kvorning et al., 2004) collected minimal and maximal pain. Yang et al. did not describe or explain which values they used.

In summary, due to its serious weaknesses in conduct, methods, and reporting, the article by Yang et al. does in our view not contribute to clarify the value of acupuncture for low back and/or pelvic pain during pregnancy but is misleading and thus does a disservice to physicians and patients.

The question raised by Juan Ervriti and Colleagues (1) whether the obvious benefit of evolocumab is offset by a currently unknown risk is justified and of high clinical relevance. We know active ingredients that effectively lower the atherogenic lipopoproteins, but have an unfavorable benefit-risk ratio under the bottom line (2). Therefore, the raised concerns must be addressed.
The chosen methodology by Ervriti and Colleagues seems to me feasible, although not perfect. For a comprehensive reanalysis the raw data are required. Unfortunately they never received such data, although they have made many efforts to do so.
To my opinion, scientific misconduct – as intended by Sabatine et. al. (3) - is not the case with Evriti et al. but rather with the FOURIER authors and the study sponsor, who apparently never answered the questions that were put to them repeatedly and publicly (4).
The announcement by the FOURIER authors that they will respond to the accusations now promptly (3) is no longer sufficient. They are biased in a number of ways, but primarily because their scientific reputation is at stake. There is no other way to understand their rude reaction.
From my point of view, it is also highly irritating that neither EMA nor Health Canada seem to have scrutinized the case report forms (CRF) when they approved this new drug. It looks like they've never laid their hands on a FOURIER-CRF. If that is the case, then they trusted the investigators blindly and failed to do their job. This would disqualify theses institutions for a trusting reanalysis of the data.
Ultimately, only another independent reanalysis of the FOURIER raw data by a recognized independent institution should clarify the facts as soon as possible.

References:
1. Erviti J, Wright J, Bassett K, Ben-Eltriki M, Jauca C, Saiz LC, Leache L, Gutierrez-Valencia M and Perry TL. Restoring mortality data in the FOURIER cardiovascular outcomes trial of evolocumab in patients with cardiovascular disease: a reanalysis based on regulatory data. BMJ open. 2022;12:e060172.
2. Rossouw JE, Anderson GL, Prentice RL, LaCroix AZ, Kooperberg C, Stefanick ML, Jackson RD, Beresford SA, Howard BV, Johnson KC, Kotchen JM, Ockene J, Writing Group for the Women's Health Initiative Investigators. Risks and benefits of estrogen plus progestin in healthy postmenopausal women: principal results From the Women's Health Initiative randomized controlled trial. JAMA. 2002;288(3):321.
3. Marc S. Sabatine, MD, MPH, Stephen D. Wiviott, MD, Anthony C. Keech, MD, Peter S. Sever, PhD, FRCP and Robert P. Giugliano, MD, SM. Letter to the Editor RE: "Restoring mortality data in the FOURIER cardiovascular outcomes trial of evolocumab in patients with cardiovascular disease: a reanalysis based on regulatory data". BMJ Open. 2022;12:3060172.
Published on: 11 January 2023
4. Erviti J, et al. Restoring mortality data in the FOURIER cardiovascular outcomes trial of evolocumab in patients with cardiovascular disease: a reanalysis based on regulatory data. BMJ Open 2022;12:e060172. doi: 10.1136/bmjopen-2021-060172

Conflicts of Interests: None