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I’ve led a small research project with another researcher. I’ve proposed a certain approach to a problem, but in fact, this approach doesn’t work, as even its simplest toy version doesn’t work. In retrospect, this toy problem should have been tested right after my part of algorithm was completed, so that two months of my co-worker’s subsequent effort wouldn’t be wasted. But coming up with such a toy problem wouldn’t be possible given the level of our experience, and especially this is my first group project.

Is this kind of situation common? How do I deal with it?

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    There is no failure, only feedback: This is nowhere as true as in science. – Mayou36 Dec 25 '17 at 10:57
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    Failing only means : try some new approach instead of the one which didnt work. – mathreadler Dec 25 '17 at 12:37
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    Although the research did not end with the expected result, it still adds value to the field, right? Now there is one less possible path to go down. – Thomas Carlisle Dec 25 '17 at 13:51
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    @Math.StackExchange I have no right to advice in research, since I am highly inexperienced.But from a simpler viewpoint, we do wish to see a lot of honest researchers.Success or failure,I personally dont care. Reason being, only such honest minds can bring phenomenal changes, since the intention is purer compared to someone who might do it for commercial success.Good hearted people fail, more often. Good hearted people contribute to the world more often, Correlation between good hearted people and success is very low, but not zero. Also, you could document reasons for failure and use it. – Rahul Dec 25 '17 at 16:03
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    Thanks everyone for changing my perspective. I will investigate a related problem to use this experience. – Math.StackExchange Dec 26 '17 at 8:14
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Failure is intrinsic to science: how can you think of exploring the unknown without ever failing? Alas, it's a certain modern, distorted, entrepeneurship view of science that brought us thinking that science should always be successful.

For my master's thesis, my PhD thesis and part of my subsequent research, I worked on an experiment that eventually didn't work. Ten years. But I learned a lot, and now that more than ten years have passed from the moment I realized the failure, I don't regret it.

So, don't be discouraged and focus on what you have learnt and not on the failure.

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    Failures should lead to papers. Unfortunately, in computer science there are far too few papers saying "We tested approach X to problem Y, and it does not work for reason Z." – Patricia Shanahan Dec 25 '17 at 9:29
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    Implicit in this answer is either a) your 'failed' project was nonetheless productive in terms of papers, or b) you had other, more successful projects with which to sustain your career. I say this because "failures pay out in lessons learned" is frequent succor here, yet lessons learned do not pay bills or satiate the pressure to produce – benxyzzy Dec 25 '17 at 22:20
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    Thankfully, this failure doesn't really affect my career. It just affected me emotionally, since it wasted my worker's time. I don't really mind about my time wasted, since I'm used to personal failures. The answers I've received changed my perspective. I will exploit my experience of failure as much as possible to be productive. – Math.StackExchange Dec 26 '17 at 8:19
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    @benxyzzy You're right, I had other projects, but they were, too, long-term projects and could not guarantee enough scientific output. This strained and eventually led to a breakup in the relationship between me and the PI, who was also my former PhD advisor, because I thought that our group should have had more short-term projects to assure a relatively steady scientific output. Since then, I changed field but, as I said, I don't regret that experience even though it had some unpleasant consequences on my career (but I got tenure right after the PhD, so I wasn't too worried). (cont.) – Massimo Ortolano Dec 26 '17 at 11:53
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    The above part, however, was a consequence of the PI's goals and should not be generalized, and that's why I haven't told the whole story in the answer. Anyway, I strongly encourage anyone, especially at the postdoc level and beyond, to have several projects in parallel, both to boost the scientific output and also to broaden the scientific interests. – Massimo Ortolano Dec 26 '17 at 11:53
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I would take it as a lesson on strategic planning and move forward. I grasped from my first supervisor that even in the small group there must be certain sub-projects planned according to BCG-matrix (yes, this marketing scheme works surprisingly well beyond business-models). Going va banque with a single idea or focusing on one problem is never a safe strategy, there always must be a fallback option.

Let me illustrate with the planing for the research group in chemistry using this terminology:

  • "Cash cows": steady income of results from a well-established procedure. Usually the results of analysis of homologous components (spectroscopic studies, x-ray diffraction, etc.), or continuous collaborative work.
  • "Stars": sudden success in complex synthesis resulting in a new compound with outstanding properties. The process is tedious, random and requires skillful scientists, but pays off a lot when finally works.
  • "Question marks": observed side-effects in certain reactions which look suspiciously interesting, but might need further investigation.
  • "Dogs": ideas which kind of work, but are trivial or hard to reproduce, or obtained using obsolete experimental technique or equipment.

Obviously, "cash cows" is a must-have, that is the only reliable option on the chart. Even if you start from scratch, do some related work aside to have a back up option. If you have talented and/or motivated people in the group, assign some of them to the "stars", but by no means the entire group. "Question marks" should be noted and kept track on in the background; often they are turning into "dogs", but sometimes they can be reassigned to the "stars".

This assures that either way you have some positive results at the end to present or even to publish. Also, you cover the entire field of your scientific interest, assuring your approach is complete and accurate in details. Long story short: manage, prioritize and divide.

One more thing: if I have a student assigned for a period longer than 3–4 months (typically to accomplish MSc, rarely BSc project), I'd usually ask how this person would like to work:

  • Intensively: focus on a specific problem which involves complex sequential actions. Implies in heterogeneous working environment. Best fit for future "stars" projects. For example: synthesize, analyze and find the single-crystal structure of a new compound X. This requires work in different labs using various methodologies and contacting a lot of people.
  • Extensively: perform routine parallel actions. Implies homogeneous working environment. Best fit for "cash cows" projects, also for students who are just passing by (not interested in a subject, but have to attend and perform). For example: spectrophotometric titrations or try-and-error syntheses. This implicates similar day-to-day activities with a little deviation in skill set.

I noticed this often helps to partially sort out psychological issues (e.g. between introverts and extroverts in a group), and people feel that they are treated more or less fairly from the beginning.

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    Portfolio optimization in which individual research efforts are considered investments seems like a really neat framework for modeling risk-vs.-reward in group management. – Nat Dec 25 '17 at 10:28
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    That's one of the better ideas I have read here in the last months. Something to try for 2018! – xLeitix Dec 26 '17 at 9:53
  • Ok so cows and dogs, got it, but what about goats and cats? – mathreadler Dec 26 '17 at 23:23
  • @mathreadler What about them? – andselisk Dec 26 '17 at 23:31
  • @andselisk where in the classification of research would they fit? – mathreadler Dec 26 '17 at 23:32
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This failure might not be enough material for a paper, but please be sure to mention this experience during your next presentations.

It doesn't have to last more than a minute at the start of your talk. Experienced researchers will smile because you've lost "only 2 months" and younger researchers will be happy to learn that failure is part of the process. It wouldn't be called research if every single attempt worked flawlessly.

After this honest introduction, listeners might be more inclined to hear what you have to say because they will know you are not only here to blow your own trumpet and lie by omission.

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Yes it is common. However it is uncommon people to acknowledge the failure, rather, they will issue statements like "a lot of progress has been made on ..." or "unlocking the potential of ... is closer than ever". Remember that you will be evaluated by non-specialists (like administrators, students, etc), which would interpret such an acknowledged failure as lack of scientific acumen.

You are on the right path if you know what has gone wrong, and you have ideas on how to solve the problem. Keep trying, that's all science is about. If you don't know how to continue, you are in disarray, and hopefully you will leave this state behind.

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