Response

We were delighted to see the findings of this impressive trial published, and we applaud the authors for delivering such a complicated study. ^{Reference Vijayakumar, Pathare, Jain, Pandit, Lohumi and Kalha1} We were, however, concerned about certain methodological and reporting issues which weakened the findings such that the conclusions drawn were not supported, nor were some of the recommendations.

Regarding the ascertainment of their prespecified primary outcome of fatal and non-fatal self-harm, the ratio of suicide deaths to attempts in the control arm during the pre-intervention period (38 of 68, 1:2) was far lower than that observed in previous studies in Gujarat, which estimated a ratio closer to 1:9. ^{Reference Amudhan, Gururaj, Varghese, Benegal, Rao and Sheehan2} This indicates that 80% of suicide attempts were missed. The authors were aware of this limitation of their surveillance in 2020, and it is surprising that efforts were not made to rectify this potentially avoidable problem. ³ Also it appears that neither the data collectors nor the informants for the trial were blinded to the intervention arm, which may have influenced the likelihood of reporting on outcomes differentially by trial arm.

Second, probably due to the impact of the COVID-19 pandemic, the assessment of outcome was severely delayed for some villages. The first intervention village would have received their intervention in November 2019, with several others having their intervention shortly after this (see the Supplementary material ^{Reference Vijayakumar, Pathare, Jain, Pandit, Lohumi and Kalha1} ). However, the analysis is based on data collected during the same 12-month follow-up period, starting in January 2022, for all villages. For the first villages, this would have been at least 2 years from the start of intervention delivery. Given that the effects of at least some facets of the intervention programme would be expected to wane over time, it becomes less credible that the intervention is the cause of any differences between the study arms after such a long period of time. Additionally, the duration of the intervention would also have differed across villages and influenced any observed effects. Although this was highlighted in the discussion, further insights may have been gained by exploring these factors in sensitivity analyses.

Third, given that for one intervention (i.e. community pesticide storage) the intended target was a reduction in pesticide-related self-harm, it is surprising that even though data on methods of suicidal behaviour were collected, the impact on pesticide-related suicide or attempts was not assessed as a prespecified secondary outcome. This appears to be a significant oversight, because the effects of community pesticide storage would be most apparent on pesticide-related self-harm, and data on the methods of self-harm would give insights into how any intervention effects were achieved.

Fourth, the randomisation of the trial occurred prior to the villages being recruited to the study, with eight intervention villages refusing to take part and not providing data. Table 1 indicates that balance was not achieved with differing baseline rates of the outcome, making it difficult to attribute differences in outcome between the study groups to an effect of the intervention. Although the authors adjust their treatment effect estimates to control for any confounding allowed by the baseline imbalance in self-harm events, confounding could still occur if the eight villages refusing to participate, having been allocated to the intervention arm, introduced other baseline imbalances – in village socioeconomic status, for example.

Our final concern is that in neither the trial registration, protocol ^{Reference Pathare, Shields-Zeeman, Vijayakumar, Pandit, Nardodkar and Chatterjee4} nor current paper do the authors specify clearly that suicide and suicide attempts as separate outcomes would form part of either the primary or secondary outcomes to the trial. Nevertheless, these are presented within the paper and given great prominence by being stated in the abstract, results and discussion. Changing the presentation of outcomes in this way, once the results have been seen, greatly inflates the risk of drawing a false conclusion that evidence of intervention effectiveness has been observed. Additionally, the weak evidence that is presented in support of a potential reduction in suicide deaths in the intervention arm, is driven by a rise in the rate of suicide in the control arm compared with a steady rate of suicide in the intervention arm. Given this, and the methodological limitations listed above, we were disappointed to see how the authors presented their findings. Concluding in the abstract that ‘[t]he intervention… reduced suicide deaths’ and in the discussion that ‘the intervention villages had a 43% lower risk of suicide deaths at 12 months’ is potentially misleading. A much more cautious approach is needed, given the serious implications of promoting potentially ineffective or inferior suicide prevention strategies, and reporting should align with the registered protocol.

Major pesticide companies are opposed to the banning of their products and have invested considerable effort to promote policies of ‘safe’ storage of pesticides for suicide prevention. ^{Reference van Schalkwyk, Collin, Eddleston, Petticrew, Pearson and Schölin5} In this context especially, the presentation of the intervention programme as effective, alongside the claim that bans of pesticides would face too many ‘hurdles’, is deeply problematic because we know that banning highly hazardous pesticides is achievable and leads to reductions in suicide deaths. Advocating for the ‘short-term’ strategy of implementing community storage, when effective and evidence-based measures such as bans are available, risks delaying the very policy change that is needed to save lives.