Introduction: A Commitment to Greatness

Before I dive into my reflections on Richard Hamming's insightful talk, "You and Your Research", I want to start by posing three critical questions to myself:

1. What are the important problems in my field?
2. What important problems am I working on?
3. If what I am doing is not important, then why am I working on them?

These questions are not meant to be answered once and then forgotten. They are meant to be a constant guiding light, a daily reminder of the higher purpose that drives my work. To that end, I am making a commitment to myself to recite the following two sentences out loud every single day:

1. Yes, I would like to do first-class work.
2. Yes, I would like to do something significant.

By keeping these aspirations front and center in my mind, I hope to cultivate the focus, the courage, and the resilience necessary to tackle the most important challenges in my field and to make a real and lasting contribution.

In this post, I want to reflect on an article that I have read multiple times and that never fails to inspire me: Richard Hamming's "You and Your Research". Despite focusing on how to do first-class, outstanding research in science, Hamming's wisdom offers invaluable lessons that can be applied to all aspects of life. His words constantly provoke me to examine how I allocate my time and effort.

This post is as much a summary of Hamming's key insights as it is a letter to myself - a reminder of the mindset and habits I must cultivate if I wish to do great, impactful work. I am writing this because, if I'm being honest with myself, I am struggling to do even mediocre research, let alone groundbreaking work. But I firmly believe that engaging with Hamming's ideas can help me break through my current limitations. I don't know if I will succeed in doing great research, but I owe it to myself to try. At the very least, I want to experience what it feels like to strive for excellence with every fiber of my being, regardless of the outcome.

Hamming structures his essay around two key questions: (1) What makes someone do great research when others do not? and (2) Why do people with tremendous promise often fail to live up to their potential? In pondering these questions through the lens of my own experiences, I hope to extract actionable lessons that can guide me on my own quest for greatness.

Part One: The Makings of a Great Researcher

Let's begin by examining the first question. Through stories of renowned scientists like Richard Feynman, John Tukey, Claude Shannon, and John Pierce, as well as his own experiences, Hamming identifies several key traits that set apart those who achieve greatness.

• Luck. One factor that Hamming discusses at length is the role of luck. He strongly believes that "luck favors the prepared mind." While chance undoubtedly plays a part in any significant success, it is not the only determinant. Hamming argues that if someone consistently does great work over a long period, there must be more than just luck at play. Individuals can create their own "luck" by being thoroughly prepared to seize opportunities when they arise.
• Drive. Being prepared is not enough on its own. Hamming emphasizes that great researchers also possess an incredible drive and an unwavering commitment to their work. They are willing to put in the long hours and make the necessary sacrifices. Hamming puts it bluntly: if you treat research like a relaxed fixed-hour job, you're not going to achieve greatness. Profound insights often come when a problem is percolating in the back of your mind, even when you're not actively working on it.
• Emotional commitment. This level of commitment requires more than just time; it demands emotional investment. Outstanding researchers are deeply engaged with their work, not just intellectually, but emotionally. This reminds me of my own experience working on my Ph.D. dissertation. I was grappling with a complex programming challenge, and the solution often came to me not when I was sitting at my computer, but when I was taking a walk or just waking up in the morning. The problem was always with me, even in my subconscious.
• Important questions. Hamming's insistence on the importance of problem selection resonates with me deeply. It's not enough to work hard; we must also work smart. He suggests that we should always be asking ourselves three key questions:
  1. What are the important problems in my field?
  2. What important problems am I working on?
  3. If what I am doing is not important, then why am I working on them?

Keep in mind that we are talking about first-class, outstanding work, not just good work. I want to add one more question here: What is my field, really? First, I need to clearly define my field. If I don't know what my field is, there is no point in asking the other three questions. These questions should guide my research direction.

However, identifying important problems is not always straightforward. Some problems may seem important but lack a feasible approach. While I can't use Hamming's Nobel Prize-worthy criterion for importance, I should still critically evaluate the significance and relevance of my work to my field. One question I can ask is: Will my work meaningfully advance my field?

• Working conditions. Richard Hamming argued that the best working conditions you desire might not be the most conducive for doing great work. He pointed out that historically, less-than-ideal circumstances often drove scientists to be more innovative, work harder, and devise groundbreaking solutions. Hamming cited the working conditions during World War II as an example, a period that saw numerous remarkable scientific advances. He also related this to his own experience at Bell Labs, where he never had all the computing resources he wanted. This limitation forced him to be creative with what he had, leading to novel problem-solving approaches and, consequently, new questions and solutions.
• Working with the system. We all have limited time and energy, so we must be strategic about where we direct our efforts. When it comes to doing great work, the choice is clear: we should focus on tackling important problems and producing excellent research. This involves learning to work within the constraints of the system and leveraging its resources, rather than fighting against it. Engaging in battles with the system only drains the energy and time that could be spent on critical work. While brilliant individuals may occasionally challenge the status quo, they quickly adapt if they realize it's a losing battle. In academia, this is less of a concern, as faculty members often enjoy a high degree of autonomy and flexibility. In most cases, the system is quite supportive.
• The importance of questioning. One of my key takeaways from Hamming's talk is the crucial role of continuously asking questions. He emphasized the importance of questioning not only his own work but also the research of others. Hamming constantly asked various questions, such as "Why?", "What do great scientists do differently?", "How did they achieve this?", "How can I turn a weakness into a strength?", and "How can I reframe an obstacle/challenge as an opportunity?" This relentless curiosity and willingness to challenge assumptions are essential for pushing the boundaries of knowledge.
• Challenges vs. Opportunities. Hamming pointed out that there are two ways to approach challenges. The first is to give up, believing the problem is too difficult, and move on to something easier. The second is to reframe the challenge as an opportunity by looking at it from a different perspective. While this shift in mindset is easier said than done, it's a powerful tool for tackling seemingly intractable problems. If you conclude that a problem is indeed too hard, don't just abandon it. Instead, ask yourself, "Why is it so hard?" or "What makes it so challenging?" By doing so, you transform the original problem into a new one, turning a roadblock into a potential breakthrough.
• Great Thoughts Time. Hamming dedicated his Friday afternoons to pondering the big questions in his field. He asked himself things like, "What will be the impact of computers on science in the future?" and "What can I do to increase the importance of computing in science?" Inspired by this practice, I can think of at least three questions to explore during my own "Great Thoughts Time":
  1. Where is my field going?
  2. Where are the opportunities?
  3. Given those opportunities, what are the important things to do?

While it may feel premature to contemplate these weighty questions when I'm still struggling to produce even mediocre research, I believe it's crucial for anyone aspiring to do high-quality work to engage with them regularly. By examining how my current research aligns with the larger trends, opportunities, and challenges in my field, I can ensure that I'm directing my efforts towards the most impactful areas. If I find that my work is not well-aligned, I can start to strategize about how to pivot towards more important problems. Having a clear sense of purpose and direction can be a powerful motivator, helping me stay focused on the things that matter most.

• Lifecycle. Hamming discussed how the age at which scientists make their greatest contributions varies across fields. In the hard sciences, it's often the young who make the most groundbreaking discoveries. However, in fields like music, politics, and literature, it's more common for older individuals to produce their most remarkable works. Hamming attributed this difference to the fact that once scientists become famous for their early achievements, they often get bogged down with administrative duties and committee work, leaving less time for focused research. Moreover, there's an expectation that they will only tackle grand challenges, making it harder for them to work on the smaller, more incremental problems that can lead to big breakthroughs. While this lifecycle effect may not be directly relevant to those of us who have yet to make our mark, it's something to keep in mind as we progress in our careers.
• Work hard and work smart. This section of Hamming's talk resonates with me deeply, as I've been grappling with the challenge of working more intelligently. While I consider myself one of the hardest-working people in my organization, I know that effort alone is not enough if I'm not directing it towards the right problems.

Hamming emphasized that hard work is necessary but insufficient for doing great research. Yes, tackling an important problem requires intense focus and dedication. When you're committed to a problem, you must be willing to put other things aside and fully immerse yourself in it. This often means consciously and subconsciously working on the problem day in and day out, even if it means neglecting less critical tasks. However, this single-minded focus shouldn't come at the expense of your health or family, as those are essential for long-term success and fulfillment.

But as Hamming pointed out, raw effort is not enough. You also need to work intelligently. If you pour your energy into the wrong problem, you'll end up wasting time and having little to show for it. That's a truly disappointing outcome after investing so much of yourself into your work. To avoid this pitfall, you need to think strategically about how to allocate your efforts for maximum impact.

One key insight from Hamming is that knowledge and productivity compound over time, much like interest in a bank account. If you consistently invest just one more hour per day than your peers, the cumulative effect can be enormous. Over the course of a career, this extra effort can result in a vastly larger body of work and a deeper understanding of your field. The following quote from the talk is one of my favourites on this point:

" 'Knowledge and productivity are like compound interest.' Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity. It is very much like compound interest. I don't want to give you a rate, but it is a very high rate. Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime."

• Sell your work successfully. Hamming argued that to make a real impact, it's not enough to do great work; you also need to be able to communicate it effectively to others. He outlined three key strategies for "selling" your work:
  1. Write clearly and compellingly.
  2. Give engaging formal talks.
  3. Give informal talks.

When it comes to writing, Hamming stressed the importance of putting yourself in your audience's shoes. When readers come across your work, what will make them pause and read it more closely? What will motivate them to prioritize your work over the many other demands on their time and attention? To cut through the noise, you need to write in a way that is both clear and compelling.

Engaging talks are another critical tool for disseminating your work. Hamming encouraged researchers to focus on giving broad, accessible talks rather than just diving into the technical details. Your goal should be to help your audience understand the big picture: what you've done, why it matters, and how it fits into the larger landscape of your field. Of course, delivering a compelling talk requires practice. Hamming emphasized the importance of rehearsing your presentations thoroughly, especially for high-stakes events.

I must admit that this is an area where I have a lot of room for growth. Too often, I've found myself rushing to put together presentations at the last minute, relying on my knowledge of the material to carry me through. But as Hamming's advice makes clear, this approach is short-sighted. No matter how groundbreaking your work might be, it won't have the impact it deserves if you can't communicate it effectively to others.

I've had the experience of giving a truly well-prepared talk, one where I took the time to think about my audience, refine my message, and practice my delivery. The difference in reception was noticeable. People were more engaged, asked more thoughtful questions, and seemed genuinely excited about the implications of my work. It was a powerful reminder of the value of investing time and effort into the communication side of research.

Going forward, I want to make a commitment to myself to prioritize this aspect of my work. I need to start my presentations earlier, seek out feedback from colleagues, and practice my talks until I feel confident in my ability to convey the significance of my work. I also want to look for more opportunities to share my research informally, whether it's through hallway conversations at conferences or casual chats with collaborators. By developing my communication skills alongside my research abilities, I can increase the visibility and impact of my work and hopefully open up new opportunities for collaboration and growth.

Ambiguity. Hamming noted that the most important problems often involve a degree of ambiguity. If a problem is too well-defined, it's likely that it's not very significant. On the other hand, if a problem is too vague or fuzzy, it may be impossible to make meaningful progress on it. The key is to find a balance between clarity and ambiguity, to identify problems that are specific enough to be tractable but open-ended enough to allow for creative insights and novel approaches.

Hamming captured this idea perfectly when he said, "If you believe too much you'll never notice the flaws; if you doubt too much you won't get started." In other words, if you're too certain about your approach or your understanding of a problem, you may miss important subtleties or opportunities for improvement. But if you're constantly second-guessing yourself, you may never take the decisive steps needed to move forward.

This concept of productive ambiguity is something I've struggled with in my own research. I often find myself drawn to problems that are either too straightforward or too ill-defined. In the former case, I can make rapid progress but the work often feels incremental and unsatisfying. In the latter case, I can spend endless hours exploring different angles and ideas without ever converging on a concrete plan of attack.

What I'm learning, slowly but surely, is the importance of embracing ambiguity while also imposing enough structure to make the problem manageable. This might mean starting with a fuzzy, high-level question but then breaking it down into smaller, more well-defined subproblems. Or it might mean setting clear milestones and deadlines for myself, even if the ultimate destination remains uncertain. By finding this balance between open-endedness and specificity, I can create the conditions for the kind of deep, sustained work that leads to real breakthroughs.

Is greatness worth it? Hamming's answer to this question is an unequivocal yes, and I couldn't agree more. In fact, his response is one of my favorite passages from the entire talk:

"I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion."

There's so much wisdom packed into these few sentences. Hamming is reminding us that the pursuit of excellence is inherently meaningful, regardless of the outcomes. It's the process of striving, of pushing ourselves to the limits of our abilities, that shapes us and gives our lives purpose. The external rewards - the recognition, the accolades - are just icing on the cake.

This idea resonates deeply with me as I reflect on my own journey as a researcher. There have been many times when I've felt discouraged, when the problems I'm working on seem intractable, or the progress feels slow. But in those moments, I try to remind myself of the inherent value of the struggle. Every challenge, every setback, is an opportunity to learn and grow, to become a better version of myself.

Of course, this doesn't mean that the outcomes don't matter at all. We all want our work to have an impact, to make a difference in the world. But as Hamming suggests, that impact is often a byproduct of the effort we put in, not the primary goal. By focusing on the process, on the daily grind of doing our best work, we increase the chances of achieving something truly meaningful.

In a culture that often celebrates overnight success and instant gratification, Hamming's perspective is a refreshing counterpoint. It's a reminder that the things worth doing are often the hardest, that true fulfillment comes from the pursuit of excellence for its own sake. And while that pursuit can be daunting at times, it's also deeply rewarding in ways that go beyond the external markers of success.

So to anyone who is struggling with the challenges of doing creative work, who is wondering if the effort is worth it, I would echo Hamming's advice: keep going. Embrace the struggle, take joy in the process, and trust that the dividends will come in their own time. The pursuit of greatness is always worthwhile, even if the path is long and the destination uncertain.

Summary of the first part. In exploring what makes someone do great research, Hamming identified several key factors. Luck certainly plays a role, but it's not just a matter of chance. Rather, luck favors the prepared mind. Those who are ready to seize opportunities when they arise, who have the drive and the stamina to pursue their ideas relentlessly, are more likely to experience those lucky breaks that can lead to groundbreaking discoveries.

But even more important than luck is the willingness to work on the important problems, the courage to tackle the most important and challenging questions in your field. This requires a deep understanding of what's been done before, a clear sense of where the frontiers of knowledge lie, and the creativity to see old problems in new ways. It also requires the judgment to know which problems are worth pursuing, even if they're not the easiest or most obvious ones.

Of course, tackling big problems demands more than just intellectual firepower. It requires an incredible level of dedication, the willingness to work long hours and make personal sacrifices in pursuit of a larger goal. But as Hamming pointed out, raw effort alone is not enough. You also need to work smart, to be strategic about how you allocate your time and energy. This means focusing on the most important tasks, collaborating with the right people, and constantly looking for ways to work more efficiently and effectively.

Ultimately, what sets great researchers apart is their ability to combine all of these qualities - luck, judgment, dedication, and efficiency - in the service of something larger than themselves. They're driven by a deep curiosity, a desire to understand the world more fully and to use that understanding to make a difference. And they're willing to put in the hard work, day in and day out, to turn that vision into reality.

For me, this summary is both inspiring and daunting. It's a reminder of the incredible heights that are possible when you combine talent, hard work, and a commitment to excellence. But it's also a challenge, a call to hold myself to a higher standard and to strive for something more than just incremental progress. As I continue on my own research journey and other journeys in life, I want to keep these lessons in mind, to stay focused on the big questions and to never lose sight of the larger purpose behind my work.

Part Two: The Pitfalls of Unfulfilled Potential

Next, let us move onto the second part of the talk: Why do people with great promise fail to do great work. Hamming provided several compelling reasons, which I will explore in more depth below.

• Lack of drive and commitment. As discussed earlier, the people who do great work possess an unwavering drive and deep emotional commitment to their work. This level of dedication is absolutely necessary for producing world-class results. If you treat your work as a 9-to-5 job, clocking out as soon as the day is over and not giving it another thought until the next morning, you might be able to do good work, but you will not achieve greatness. There is a vast difference between merely good work and truly great work. Hamming put it eloquently: "The people who do great work with less ability but who are committed to it, get more done than those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day."
• Not working on important problems. Some people fail to do great work because they simply aren't tackling the important problems in their field. They might be investing their time and energy into trivial or tangential issues rather than focusing on the core challenges that have the potential to drive significant advances. In some cases, they may believe they are working on important problems, but they haven't critically examined their assumptions or sought out external perspectives to validate the significance of their work.
• Making excuses. When confronted with the question of why they didn't achieve a particular breakthrough or make a key discovery, some individuals resort to making excuses. They claim that they could have done it, but some external factor or circumstance prevented them from getting there first. Rather than taking responsibility for their own choices and actions, they blame their failings on outside forces.
• Failing to reframe challenges as opportunities. Great scientists have a knack for transforming apparent obstacles or deficiencies into advantages. Instead of complaining about the resources they lack or the roadblocks they face, they find creative ways to work with what they have and turn faults into features. They approach problems from novel angles, redefining the questions or constraints in ways that open up new possibilities. Less successful researchers, on the other hand, tend to get stuck when confronted with difficulties, seeing them only as insurmountable hurdles rather than chances to innovate. They then move onto a new easier problem.
• Letting ego get in the way. Ego can be a major barrier to doing great work. When researchers become more focused on asserting their own brilliance or defending their turf than on pursuing the truth, they waste valuable time and energy that could be directed towards the actual substance of their work. Hamming noted that this ego-driven behavior exacts a steep cost, even if it may feel gratifying in the moment. Over the course of a career, the toll of constantly battling to prove one's superiority can be immense, sapping the resources and motivation needed for deep, sustained work on important problems.
• Fighting the system instead of harnessing it. Some researchers expend a great deal of effort fighting against the constraints or incentive structures of the systems in which they work, seeing them only as impediments to their goals. While there may be times when the system needs to be challenged or reformed, Hamming argued that great scientists are usually more strategic in their approach. They find ways to operate effectively within the existing framework, leveraging the resources and opportunities it provides while minimizing unproductive friction. They pick their battles carefully, rather than letting themselves get bogged down in constant conflict.

Ultimately, the key differentiator between those who fulfill their potential for greatness and those who fall short seems to be a combination of focus, resilience, and adaptability. The most successful researchers are able to identify the truly consequential problems, and they pursue them with a singular passion and determination. When they encounter setbacks or constraints, they find creative ways to circumvent or exploit them, rather than getting discouraged or side-tracked. They are able to sustain their momentum and motivation over the long haul, making steady progress even in the face of obstacles.

Hamming's observations serve as a powerful wake-up call, urging me to interrogate my own practices and assumptions more rigorously. If I want to have any hope of making a real contribution, I need to be brutally honest with myself about where and why I'm falling short and what I need to change. This doesn't mean beating myself up for my failings, but rather using them as a spur to continual growth and improvement. By keeping Hamming's lessons at the forefront of my mind, I can hopefully avoid some of the common traps that hold researchers back and put myself in a better position to achieve something truly meaningful.

Insights from the Q&A: Practical Wisdom for the Journey

The Q&A session following Hamming's talk offered several additional insights that are worth reflecting on.

• The role of stress. Hamming acknowledged that stress is an inevitable part of doing great work. If you're not feeling any stress, it's likely that you're not working on problems that are truly important or challenging enough. Of course, there's a difference between the healthy stress that comes from pushing yourself outside your comfort zone and the toxic stress that comes from overwork, burnout, or a dysfunctional environment. But a certain amount of tension seems to be necessary for driving creativity and breakthrough thinking.
• Balancing reading, writing, and research. Hamming shared his own rough breakdown of how he allocated his time: in the past, it was about 50% on reading and writing and 50% on doing research, but more recently, he found that presenting his work took up at least half of his time. This underscores the importance of communication and dissemination as integral parts of the research process, not just afterthoughts. It also highlights the need to be intentional about carving out dedicated time for deep work, even as other demands on our time and attention multiply.
• Risk-taking in a competitive environment. An audience member noted that young researchers today seem less willing to take risks, perhaps because of the intense competition for funding, positions, and prestige. Hamming acknowledged this trend, contrasting it with the more free-wheeling and daring spirit of his own early career in the 1940s and 50s, particularly during wartime. While he didn't offer any easy solutions, he seemed to imply that we need to find ways to create environments that encourage and reward bold, unconventional thinking, even if it doesn't always pan out in the short term.
• Getting an effect named after you. When asked about how to cement one's scientific legacy, Hamming had a simple answer: do great work. If you make a truly fundamental contribution, people will remember and honor it. But the goal should be the work itself, not the accolades that might come with it.
• Approaching the literature. Hamming had some characteristically provocative advice about how to read the scientific literature. He argued that once you've clearly defined your problem, you should stop reading and start thinking for yourself, working out your own approach before diving back into what others have done. The literature is there to help you sharpen your understanding of the problem, but it shouldn't dictate your solution. Here's the key quote:

"If you want to think new thoughts that are different, then do what a lot of creative people do - get the problem reasonable clear and then refuse to look at any answers until you've thought the problem through carefully how you would do it, how you could slightly change the problem to be the correct one."

This is a powerful idea, and one that I've been trying to apply more in my own work. Rather than just immersing myself in what others have done and trying to carve out some incremental contribution, I'm striving to first get clear on what I think the real problem is and how I would approach it if I were starting from scratch. Only then do I map my fresh perspective onto the existing landscape to see where the gaps and opportunities lie.

• Avoiding stagnation after success. Another audience member asked about how to keep making progress after an initial breakthrough, when the temptation might be to rest on one's laurels. Hamming suggested that one way to stay motivated and avoid falling into a rut is to change fields every seven years or so. Not a drastic shift, like from physics to poetry, but a deliberate move into an adjacent area where you can bring fresh insights and be pushed out of your comfort zone. This requires humility, because it means going back to being a beginner in some sense, but it can be a powerful way to sustain creative momentum over a long career.
• The importance of intellectual community. Hamming emphasized the value of surrounding oneself with brilliant, ambitious peers who have high expectations. The people we spend time with shape our own standards and aspirations, so it's crucial to seek out colleagues who will push us to do our best work. At the same time, I would add that it's important to find a community that is supportive and collaborative, not just competitive and critical. We need people who will challenge us to grow, but also pick us up when we stumble and remind us of our own potential.
• The prepared mind. One audience member suggested that luck had played a significant role in Hamming's own success. While he acknowledged the role of chance, Hamming argued that luck is only one factor among many - and not the most important one. Quoting Pasteur, he noted that "luck favors the prepared mind". In other words, we make our own luck by being ready to seize opportunities when they arise, by cultivating the knowledge, skills, and habits that allow us to recognize and capitalize on serendipitous moments. Luck may open doors, but it's up to us to walk through them.

Reflecting on these additional insights from the Q&A session, I'm struck by how much they resonate with my own experience as a researcher. I've certainly felt the pressure to "play it safe" and stick to well-trodden paths, especially as competition for limited resources has intensified. But I've also seen and heard how transformative it can be to take a chance on a bold idea, even if it means risking failure or criticism.

At the same time, I recognize that I could be more proactive about seeking out collaborators and mentors who will push me to raise my game - not just in terms of technical skills, but also in terms of the questions I ask and the problems I choose to work on. I'm realizing that the quality of my intellectual community is just as important as the quality of my individual efforts.

Most of all, Hamming's emphasis on the "prepared mind" strikes me as a crucial insight. It's not enough to just hope for a lucky break; I need to be doing the hard, unglamorous work of honing my craft and broadening my knowledge base every day, so that I'm ready to make the most of whatever opportunities arise. Charlie Munger says "Try to be a little wiser than you were when you wake up." This means carving out time for deep, focused work, even in the face of endless distractions and demands on my attention. It means being deliberate about what information I consume and what skills I cultivate, so that I'm not just reacting to the prevailing winds but actively charting my own course.

In the end, what I take away from Hamming's talk is not a recipe for success but a challenge to strive for greatness - not just in terms of the problems I solve or the accolades I earn, but in terms of the scientist and person I become in the process. It's a reminder that the real reward is in the struggle itself, in the daily effort to push myself beyond what I thought was possible and to contribute something of lasting value to the world. And while there are no guarantees in this business, I believe that if I can approach my work and my life with the same passion, integrity, and unrelenting commitment that Hamming describes, then I will have succeeded on the terms that matter most.

Conclusion: A Daily Renewal of Purpose

As I come to the end of this reflection on Richard Hamming's talk, I am more convinced than ever of its enduring value. This is not a piece to be read once and then set aside; it is a manifesto to be revisited and wrestled with again and again. I am making a commitment to myself to re-read this talk at least once a year - to reflect on how I am allocating my time and energy, to assess my progress towards doing truly important work, and to realign my efforts based on the insights and provocations that Hamming offers.

To hold myself accountable to this commitment, I will end each re-reading by reciting once again the two sentences that I began with:

1. Yes, I would like to do first-class work.
2. Yes, I would like to do something significant.

These are not just idle wishes or vague aspirations. They are a solemn vow to myself and to the world - a declaration of my intent to strive for greatness, to push beyond my perceived limitations, and to use my talents and energies in the service of something larger than myself. They are a reminder that the true value of my work lies not in the accolades or rewards it may bring, but in the depth of my dedication to the pursuit of knowledge and understanding.

I know that this path will not be easy. There will be setbacks, frustrations, moments of doubt, and even failure. But I also know that the struggle itself is worth it - that in wrestling with the hard problems, in pushing myself to the limits of my abilities, I will grow and evolve in ways that I cannot yet imagine. And even if I never fully achieve the lofty goals that Hamming sets out, I will have lived a life in pursuit of something noble and worthwhile.

So let me end where I began, with a reaffirmation of my commitment:

Yes, I would like to do first-class work.

Yes, I would like to do something significant.

The journey begins anew each day. Let me rise to meet it with all the passion, integrity, and determination that I can bring together.