20

Sometimes I have simple ideas that can be useful. They could be obvious or not, or it is possible that no one ever considered them the way I did.

For example:

To gather information about the statistics of the unemployed in a city or state, I suggest to build a website in which unemployed people register and enter their information. This information is very useful for decisionmakers on unemployment. But, after a while these statistics are not valid. On the other hand, unemployed people are very reluctant to update their employment status via the Internet or they don't have access to it. To solve this problem, we can send an SMS to them and they answer with 1 (as employed) and 0 (as still unemployed), then we integrate these answers to the central database. This way, we have up-to-date information in periods.

The idea was that simple, however maybe no one in our country implemented it. Could it be a paper? If yes, what can it include? Because it is as short as the above. Should I, for example, explain how we integrate the SMSs to the database (however, it may be simple too or the subject of other tools or papers). If I implement the system, should I provide the statistics of unemployment in a city or the percentage who contribute the plan? Totally, I don't know what else such a paper should cover.

For another example, suppose that I am the first one who invented the sliced bread. How long could my paper be and on what would I probably argue?


However it was just an example and after some research I may realize it is not workable, but I should say I actually built the website for an organization in my city one year ago (However not the SMS and updating part), then I was thinking if I can make a paper out of it. Maybe I could use some parts of the real data I gained in such paper, for example the people who registered (which was more than 80% of all the unemployed ranging from 20 to 40 years old) and those who had a cell phone (which was more than 98% of them), this topic shed some lights on my way.

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    I feel like almost all good ideas, feel simple to the people who come up with them. (One of the causes of Imposter syndrome, maybe). – Lyndon White Jul 10 '15 at 6:31
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    You can write a paper out of everything (actually I can write a paper about how I commented your question). The question is whether somebody will be willing to publish your paper. Looking at your suggested implementation it lacks a lot of details (why do you actually believe that unemployment people will answer everything, or will answer truthfully, what if only people who got employed will answer and you will get that everyone is employed). What you described is more suited for a github project rather than a paper. – Salvador Dali Jul 10 '15 at 9:13
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    Mate, the people who reply to the text are the ones with the jobs and those who don't reply are the one's who still can't afford phone credit, or even worse, had to sell their phones. – Kenshin Jul 10 '15 at 9:14
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    @Ahmad Cats and dogs may have cell phones, but then they don't have to pay the bills. I have known of actual people (students, in fact) who had to sell their phones due to temporary "liquidity problems". The digital divide is not only about age groups, economics can also be an issue. – ALAN WARD Jul 10 '15 at 14:33
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    If a person is unemployed and receiving unemployment benefits, then the state already has those numbers. They're only missing the unemployed who are not receiving benefits (of any sort, usually; welfare tends to want to know your employment status, for example). – zibadawa timmy Jul 10 '15 at 15:43
39

I like papers about simple ideas. (I am writing one right now, hope others like it as well.) They are far easier to communicate and understand than complex ideas.

Then again, the question is why nobody else has thought about an idea if it is all that simple. In your specific example, the idea may not be workable, because people may simply delete the update SMS without replying to it. (And those that do answer may not be representative of your sample as a whole.)

So I would say that writing a paper about a simple idea is good, but it needs to meet the same conditions as any other paper: it needs to show that the idea actually works. An idea by itself is usually not worth an entire paper. Having the idea is often the easy part. Showing that it works is where the actual work happens.

So: Build your website for one city, let it run for six months, then write a paper about what you learned.

How to show that something "works" may well be the hard part. (For instance, in some parts of machine learning it is easy to "show" that a method is better than an established method by testing both on many datasets but then only reporting those on which the proposed method is superior.) Some journals/conferences/reviewers may be more stringent about what they consider proof that something "works". You may be able to get a publication out of a proof of concept by just building the website, without running it productively. Or by running it productively, but without assessing in some way whether the statistics collected by the website are actually more accurate than those collected in some other way. Look at what kinds of papers your target venue or community publishes, and let yourself be guided by that.


EDIT 2016-04-07, about that article based on a simple idea: it turns out that this simple idea (a randomized probability integral transform) was really good. So good, in fact, that multiple people had had the same idea previously, and at least partly independently of each other. Happily enough, a guru in the field pointed this out to me when I circulated a preprint and didn't savage me, but pointed out shortcomings of the rPIT and possible new lines of inquiry. The paper has just been published.

Bottom line: your simple idea may be good, but chances are that those ideas that are both simple and good have already been worked on.

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    "Build your website for one city, let it run for six months, then write a paper about what you learned." and perhaps use a second city with a similar situation as a test group to compare results against. – ALAN WARD Jul 10 '15 at 14:35
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    By the way, I should say I built the website for an organization in my city one year ago (However not the SMS and updating part), then I was thinking if I can make a paper out of it. Maybe I could use some parts of the real data I gained in such paper, for example the people who registered (which was almost all the unemployed) and those who had a cell phone (which was more than 90% of them), this topic shed some lights on my way – Ahmad Jul 11 '15 at 18:14
  • I think you should add the info that you build the website and have the data to the question. – Toxaris Jul 11 '15 at 19:53
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No, you cannot write a paper out of a simple idea. A simple idea contributes nothing. I guess we all have simple novel ideas every day.

However, if you ground that simple idea within theory, and/or build a theoretical framework, with suitable references to existing literature, and you demonstrate that this hasn't been done before, and maybe explain why it hasn't, and suggest how it might improve on existing alternatives, then that's a paper.

If you take that theoretical grounding and then set out a plan of implementation, together with a monitoring and evaluation framework to assess its impact, together with a comparison against existing alternatives then that's a paper.

And if you implement it and evaluate it as above, then that's a paper.

If you want one higher impact paper rather than three lower-impact papers, and if journal space allows, you could do all three of those things in one paper.

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    you are right, however it depends on our expectation of papers. I see thousands of complicated papers on nonsense things in some fields. – Ahmad Jul 10 '15 at 7:19
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    I may summarize your answer with this interesting quote from @ff524 "No, you can write a paper about research but a simple idea itself is not research." – Ahmad Jul 13 '15 at 7:58
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Warning: Harsh answer following.

@energynumbers has covered some of the aspects of why a "simple" idea is not enough for a research paper. It needs prior literature search, must improve on previous methods, a theoretical justification why it should work and an experimentation section providing the benefits of the idea, compared to previous state-of-the-art.

Still, when I read your original question and your later comments, initially I thought you were joking. Without wanting to be harsh, I could not believe that sending bulk SMS to unemployed people is your idea of fighting unemployment or meaningful research. As a computer scientist myself, I try to refrain from suggesting ideas about problems I do not have not the capacity nor the knowledge or the necessary background to understand. And your comments like "even cats and dogs have cell phone" not only show you know nothing about unemployment but you are also indifferent and ignorant to this huge problem's social implications.

But let's stick to the "scientific merits" of your idea. Any EU country has an unemployment rate of (very rough estimates) 4% (Germany, Austria) to more than 20% (Spain, Greece). That means that even in countries with low unemployment rates (e.g. Germany), sending a SMS to unemployed people would require 3,4M SMS. Since, the unemployed should answer these SMS by yes or no that means another 3.4M SMS. Who will pay for those 7M SMS of your idea? Even for a big city (1M people) that would require at least 8K SMS for Germany or 20K SMS for Spain. Perhaps you are implying that the unemployed people should pay the response SMS from their pockets, for their "right" to participate in your "novel" research? You also seem to assume that all unemployed people have internet connections (for filling in their data) and cell phones, when usually unemployment benefits (if they have not expired) can only cover very basic needs. And you also want to force those unemployed people to fill another form for giving you their data (and who authorized you to collect this data? It will be probably illegal in many countries) besides registering to the respective unemployment agency and sending bulk CVs to potential employers for hoping to land their next job. This is not only insensitive but borderline silly.

Bottomline: Research is a very serious job. Not everyone can do it. Especially when there are sensitive groups and people involved. Treat it as such. If your concept of research is ideas that come to you when you are ordering french fries or you are in your bathroom during your "physical" duties, you are WRONG. Otherwise your "research" ideas would sound like the infamous French phrase "Qu'ils mangent de la brioche". They will not only lack any scientific merit but they will also sound insensitive and ignorant.

UPDATE: a) At the OP. You (and I) are no Newton. Even if someone hit you with all the apples of the world, you will most likely develop a head trauma than the theory of gravity b) As others have commented, brilliant ideas can come anytime but ONLY after studying a problem for weeks, months or year. Check the term Eureka effect, why that happens. c) Even after studying a problem for a long time, the majority of the ideas that one comes up with are not necessarily good d) Even if you come up with a brilliant idea, it needs weeks of work on pen / paper, pc or lab for that idea to actually be publishable. e) What "most people grasp" is not scientifically correct. People believed for thousands of years (some people still do) that the earth was flat and the sun revolves around the earth. So, basing your scientific ideas on "common sense" has no scientific merit. f) If you do not believe me or the others commenters, try to publish your "simple" idea and wait until the peer review replies back. Then you will have your answer.

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    I think you have hit it on the nail when talking about research being a "job". It is work, and needs to be done in a professional manner. So I agree having a good idea (simple can be good) to start with is necessary, but by no means sufficient. – ALAN WARD Jul 10 '15 at 14:39
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    @Ahmad the inspiration can come any time, but you still need a lot of work to get it into useful shape. As Picasso said, "may inspiration finds me working". – Davidmh Jul 10 '15 at 16:23
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    @Ahmad yes, I'm saying exactly that. The purpose of publishing (and in fact the essence of the academic spirit) is to expand and further humanity's potential. To help us understand reality, and do better things faster. Anyone and everyone can have an idea at any time - so what? Why does this matter to X field, and how can you prove that it's more effective than what we're doing now? Show me. Convince me. Prove it. If you can't do that with your idea, then it doesn't further your field and you shouldn't be publishing it. – CodeMoose Jul 10 '15 at 17:50
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    @Ahmad: The whole point of science is that we do not accept anything as self evident - evidence is required. Often times "most people grasp" something that turns out to be wrong. – Nate Eldredge Jul 11 '15 at 13:47
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    @Ahmad "we can't deny the simple ideas who changed the world and suggested by ordinary people, while scientist were busy with publishing complicated articles". You've made it clear you don't have patience or respect for academic rigor, and because of that I'm concerned you won't like the outcome if you do try to publish. Have you considered taking your idea to the business domain? With the right contacts, it probably wouldn't be difficult to sell. That way, you can still influence the world and become famous, without all the pesky hassle of dealing with academic integrity. – CodeMoose Jul 12 '15 at 0:48
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You can't publish "an idea" alone, whether it's simple or not (with some notable historical exceptions). I'll copy some of the things I said to someone who was trying to sub-contract the scientific work necessary to make her/his ideas worth publishing in exchange for authorship.

Ideas have very little value by themselves. The chances that they are absolutely original is very low and it's the rigorous test of their validity along with informed discussion about why they work that is worth publishing

and further down in my comments:

An idea like 'We should build space elevators!' is not worth a lot compared to 'I have made these rigorous calculations/experiments about the strength of carbon nanotubes that could, maybe, constitutes wires going from Earth to Space'

So, like Stephan Kolassa implies in his answer, it doesn't matter if the idea is simple or not, you need to test its validity in some way, whether experimental or not, to make it into a paper.

I can't think of a scientific discipline in which to put your idea (or sliced bread for what matters). I'm not sure using 1980's technology to obtain data of dubious quality would be considered a breakthrough. Nonetheless there are many things you can do with this idea other than trying to publish it, if you believe in it, like convincing your local government to hire you to implement it.

  • Thank you, while I agree, I just can't get why we should waste our valuable time on implementing and testing and comparing something that works, while our brilliant mind could search for the remaining ideas. There are engineers and programmers who do the stuff work. Why Einstein which his depth of thoughts can change a world should be busy on implementing a device to measure the time in the speeds near the light? Then it is not always implementation, but maybe mathematics, logic, literature too. While I feel today all want you experimental results – Ahmad Jul 11 '15 at 18:53
  • I feel I am kidding, I got that you all say, that publishing a paper has two parts. 1- idea, 2- defending it. – Ahmad Jul 11 '15 at 19:08
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    How to validate an idea depends on the academic field of study. Some fields require experiments, some fields require mathematical proof, some fields require careful arguments, etc. Check published papers in your field to see how they validate their ideas. – Toxaris Jul 11 '15 at 19:18
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    @Ahmad why we should waste our valuable time on implementing and testing and comparing something that works You don't know if it works. If you do then it's not a new idea. It doesn't need to be experimental. You could test a theory by checking its self consistency or by comparing its prediction with existing observations, etc. – Cape Code Jul 11 '15 at 19:51
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    If you are still unconvinced that naked ideas have little worth, try to sell them. – Cape Code Jul 11 '15 at 20:12
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Academic papers are (or should be) not really about presenting ideas, but about answering research questions. So your paper should state the question, the answer, and why the answer is true. So even if your research starts with an idea, you should ask (and answer) questions about it, such as:

  • how effective is the idea?
  • how expensive is the idea?
  • is the idea better or worse than other related ideas?
  • is the idea different or similar to other related ideas?
  • is the idea expected or unexpected given other related ideas?

The exact questions you can ask depend a bit on your idea, of course. For your example idea of sliced bread, some questions come to mind:

  • is sliced bread more or less healthy than unsliced bread?
  • how long can sliced bread be stored?
  • how expensive is bread slicing in the bakery vs. at home?
  • are customers prefering bread sliced vertically or horizontally?
  • how should a knife for slicing bread be shaped?
  • should we ban sliced bread in war time?
  • will people eat more or less when sliced bread is available?
  • how does the bread-slicing machine work?
  • how much time is sliced bread saving the average family per day?
  • overall, is sliced bread cheaper or more expensive for a society?

Scientific research is about delving deep into such detailed questions, and figuring out the actually true answer. So research is not just about asking these questions and answering them somehow, but about finding the true answer, and convincing other researchers that you found it.

Since each question usually requires substantial investigation (by experiments, computation, simulation, thinking, ...) , usually a paper will only answer one question, or sometimes you even need multiple papers just to answer one question. For example, if you ask lots of customers whether they like their bread sliced horizontally or vertically, and more say "horizontally" than "vertically", that might be a paper. Now if you actually observe lots of customers buying more vertically sliced bread than horizontally sliced bread, that's another paper. Yet another paper can then ask the question: Why do people say one thing and buy another? This way, an understanding about an aspect of the world (here: people's bread-buying preferences) is build paper-by-paper, in an collaborative effort of the scientific community.

  • Nice! thank you for pointing the example! then if I just prove that sliced breads sell more, it would be just a proposal for a company and not a scientific paper? You mean I should also consider the customer health, benefit loss....? – Ahmad Jul 11 '15 at 20:10
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    If you actually prove that sliced bread sells more, that might be a paper. If you only say that sliced bread sells more, it's not. If you just say what sliced bread is, it's not a paper either. – Toxaris Jul 11 '15 at 20:11
  • Interesting! then you mean paper 1) sliced breads sell more .. paper 2) The possible harms of sliced breads to the customers... 3) why Amricans favor sliced breads: An investigation into the psychological and social factors ... 4) The machinery required for sliced breads... These are all papers? – Ahmad Jul 11 '15 at 20:18
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    I edited the answer to make it clear that no single paper has to (or can, usually) answer all the questions. – Toxaris Jul 11 '15 at 21:17
  • Thank you, just I think some of the problems (or papers) raise after the sliced bread got widespread or justified. And I look for the first paper on the sliced bread. (I also answered the question based on your suggestion which you can find at (academia.stackexchange.com/a/48671/21885) – Ahmad Jul 12 '15 at 5:31
3

It all depends on various factors, most importantly your target audience and/or journal (or other publishing outlet) as well as, potentially your field of study. For some people, outlets and fields of study, a simple idea might be very well appropriate, when "wrapped" into a research paper format, for others it might not (either due to being too simple, that is, obvious, or due to being "wrapped" inappropriately). Obviously, it also depends on how you "wrap" your idea, in other words, what contents, level of detail and level of rigor you would employ for presenting the idea to community.

In regard to suggestions by previous answers' authors that one need to fully implement an idea and present corresponding findings, I respectfully disagree and think that for many ideas building a prototype or, even, presenting a design or architecture of a proposed system is enough for a paper (usually, that would be a working paper or a conference paper or other work-in-progress paper).

  • I also have the same feeling, for some simple idea or architecture, implementation or results, is like saying something twice. For example in the system I described above, I should waste a lot of time to finally say "Yes people prefer to update their employment status via cell phone and 90% contributed versus 50% in the usual update via internet" – Ahmad Jul 10 '15 at 7:26
  • Moreover, as I said in the question, I really don't know why I should mix many things to "wrap" a simple idea. Or what are those. Each of them may have their own subject – Ahmad Jul 10 '15 at 7:28
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    @Ahmad: You don't have to "mix many things" to "wrap" a simple idea, however, you have to have a minimal set of elements for a body of work to qualify as a research paper, as opposed to, say, blog post or a popular press article. – Aleksandr Blekh Jul 10 '15 at 9:39
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    @Ahmad Your idea only has scientific value if you can provide some evidence for your hypothesis, or, at least, very strong arguments why that may be the case. In your case, you could refer to statistics on internet access vs phone penetration in different societies have; and how well targeted employment policies are (that is, given the same budget, how much better could we be doing?). – Davidmh Jul 10 '15 at 15:00
  • @Davidmh Good advice, however they shift the paper from a "simple idea" to a research on unemployment policies and social and economical factors.... I agree, but I have problem to find the scope of each paper. (Maybe from a technical viewpoint in computer science, the application is not important and just the technical details of the implementation are wanted!) – Ahmad Jul 10 '15 at 15:34
1

I read the answers and I am going to take a different view. I think every idea should be written down as a paper. I agree with other answers that a simple idea is not suitable as a research submission etc. You also mentioned that you have now realized why your idea is not going to work. I would say that both of above conclusion (i.e. is idea going to work and if it is, then is it worthy of being called as research) should be drawn after the paper writing. Not the polished, final draft paper writing but may be after zeroth draft. Paper writing is not the culmination of research. It is an integral process of coming up with an idea, developing that idea into a testable hypothesis, carrying out experiments (real and simulated), and writing it up. You may ask that above mentioned process talks about writing at last stage so how is it an integral part? Because you should plan by writing. You should leave placeholders for data you are waiting for. If your data does not validate your hypothesis, go back to writing and draw new plan and repeat. Doing this will tell you when your idea is not going to work, writing literature review will tell you whether or not your idea is worthy of publication in good journal. It is possible that once you start writing, your paper may go in some other direction. For all this to happen, you should always write things as paper.

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I myself conclude that it follows the same common steps to write any paper, to explain them I directly go to the examples A (SMS to the unemployed) and B (sliced bread)

1) You should first ask what is the problem? An idea without mentioning a problem is lame.

  • For A) After awhile the unemployed statistics is not up-to-date and people don't update them for these reasons...

For idea B, some scenarios is possible

  • 1) Many breads is wasted because of the way people buy, store and use them
  • 2) A plan to increase the consumption of bread or jam (It looks like more a business idea? it works if bread and jam company are partners)

2) What is your idea or plan?

  • For A) Sending periodical SMS to the unemployed to gather short data

  • For B-1) Sliced bread

  • For B-2) Sliced bread

3) Then you may ask What is the contribution of this idea to my field of study?

Gathering data about unemployment using SMS, for example, might be a useful contribution to the field of economics (if it is indeed demonstrably better than existing methods), but as currently described it is not likely to be a useful contribution to computer science

4) How does it solve the problem

Description of the idea and the way it works

5) How are you sure? why it is better than other solution?

There could be several ways to show it for A:

  • Based on the statistics of cell-phone penetration in "the unemployed" their usage pattern, previous researches, arguments like "Concerning the penetration of cell phones, SMS is a cheap and effective solution to gather periodical and short data..."
  • Testing the idea in a small city and showing the results

For B: Test it on some families, or better a city

  • Do they buy it?
  • Problems with its consumption, (with which foods they can consume it)
  • Is it have any affect on you or them to consume jam more...
  • Is the cost for slicing bread compensated?
  • ....
  • Please those who down-vote, say what is wrong with the post! – Ahmad Jul 13 '15 at 5:36
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    You are missing a crucial step. You need to ask: What is the contribution of this idea to my field of study? Gathering data about unemployment using SMS, for example, might be a useful contribution to the field of economics (if it is indeed demonstrably better than existing methods), but as currently described it is not likely to be a useful contribution to computer science. – ff524 Jul 13 '15 at 6:36
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    Generally, an application that does not contribute something new to our understanding of computer science is not considered a research contribution. If you read a paper that seems like "just" an application, either (1) it's not a good paper, and probably wasn't published in a good conference or journal, or (2) you didn't understand its contribution (i.e. you didn't understand why it's more than just an "application"). – ff524 Jul 13 '15 at 6:52
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    Here is a related paper and here's another about use of SMS as a survey tool for medical applications. Note that the papers are published in a medical informatics and medical journal, not computer science. Also note that they perform a rigorous evaluation of the proposed idea, extensive survey of the literature, and more; they don't just write out an idea and call it a paper! – ff524 Jul 13 '15 at 7:08
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    To me, this answer just misses the point. The answer to your question of "Can you write a paper about a simple idea?" is "No, you can write a paper about research but a simple idea itself is not research." Your answer tries to list all the "ingredients" of research and say, "That's how to structure a paper about a simple idea," but the question of how to do research is much, much bigger than the scope of this question and answer. It can't be distilled into a simple formula, like you're trying to do. – ff524 Jul 13 '15 at 7:15

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